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Master Thesis

Anna Hasselqvist Haglund

Uppsala University

Spring Semester of 2018

Supervisor: Helena Holmlund

Public secondary school mergers as a desegregation method in Swedish

municipalities - Investigating their impact on student’s academic performance and choice of school

Abstract In recent years several municipalities in Sweden have merged their public secondary schools. This

has been considered a type of initiative that intends to reduce youth segregation and discrepancies in

school quality. This thesis examines in what ways the merging of all public secondary schools in a

municipality affects the students’ academic performance and their choice to enroll in the public-

school sector. To do so I use municipality-level aggregate data from the Swedish National Agency

for Education on 9th grade students’ academic outcomes and the share of 7th graders enrolled in the

public schools. I employ a difference-in-difference approach to estimate the reduced form effect of

the school mergers. The control group used in the baseline estimation includes all municipalities that

had a constant number of public secondary schools during the time period of my study. I move on to

use propensity score matching in order to create a more comparable control group. I then estimate a

difference-in-difference regression with match-fixed effects. The results show that the mergers have

a negative effect on the municipality-level average GPA. In addition, the municipalities where the

mergers have been implemented experience a reduction in the share of students that pass all 9th grade

subjects as well as an increase in the share of students who do not have sufficient grades to continue

to upper secondary school. The school mergers caused the share of 7th graders enrolled in the public-

school sector to decrease by approximately 10 percentage points. These results indicate that the public

secondary school merger is not a panacea for improving student outcomes.

Table of Contents

1. Introduction…………………………………………………………………………………..1

2. Background…………………………………………………………………………………..3

2.1 The Swedish education system……………………………………….……………………..3

2.2 Previous literature.……………………………………………..……...…………………...3

3. Theory……………………………………………………………………………………….6

4. Data………………………………………………………………………………………….8

4.1 Data description and coding issues……………………………………….…………….…...8

4.2 Outcome variables……………………………………………………...…………………10

4.3 Treatment and control groups………………………………………………………….…..11

4.4 Descriptive statistics…………………………………………………...………………….14

5. Method…………………………………………………………...………....………………16

5.1 Empirical framework………………………………………………..…………………….16

5.2 Underlying assumption………………………………………………..…………………..17

5.3 Matching………………………………………………………………………………....18

6. Results………………………………………………………………..……………………..20

6.1 Difference-in-difference results………………………………………………..…………..20

6.2 Matched difference-in-difference results………………………………………...………....23

6.3 Heterogeneous treatment effects……………………………………………..…………....27

7. Sensitivity analysis…………………………………………………………..……………..30

7.1 Event studies……………………………………………………………………………..30

7.1.1 Parallel trends……………………………………………………………………32

7.1.2 Dynamic treatment effects……………………………………………..…..……..32

7.2 Placebo tests on control variables………………………………………………………….33

7.3 ‘Worst case’ and ‘best case’ variables………………………………………………….......34

8. Discussion and concluding remarks………………………………………………….…….35

References…………………………………………………………………………………………..38

Appendices

A. Table of municipalities excluded from control groups…………………………………………..40

B. Table of matched control groups……… ……………………………………………………...41

C. Figure for event studies baseline panels………………………………………………………..43

D. Table of ‘worst case’ and ‘best case’ comparison………………………………………………44

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1. Introduction

The Swedish education system has long been built upon a notion of egalitarian ideals. The aim is

to offer high-quality education without selective sorting of gifted students or imposing tuition fees. At

a glance, the Swedish education system should provide a good foundation for scholarly success. Yet the

results from the 2012 PISA survey got a lot of attention as it revealed that Swedish fifteen-year olds

performed significantly worse than the OECD-mean (Swedish National Agency for Education 2013).

On a somewhat more positive note, the results from the 2015 PISA survey did show improvement in the

Swedish students’ overall academic performance. However, the survey points out that there are signs of

growing achievement gaps between high and low-performing students and among students with

different socioeconomic status (OECD 2016).

One of the possible reasons for the widening of the achievement gap is that school segregation

has become increasingly present in Sweden (SOU 2017:35). School segregation implies that students

with background characteristics that increase their probability of scholarly success attend one school,

while students with a relatively more disadvantaged background characteristics attend another. This may

have negative consequences on student performance, especially for students with a low socioeconomic

status. Furthermore, school segregation may endanger the equity goal that Sweden has set for its

education system, as it might create heterogeneity in quality among schools. One reason may be that

students with low socioeconomic status are missing out on positive peer effects from classmates with

high socioeconomic status.

In 2014 the local government in Nyköping municipality took action in an effort to increase student

achievement and promote youth integration. The municipality had four public secondary schools. For a

long time, the average grade results from one school outperformed the others. This school consisted of

students with parents of Swedish descent living in predominantly high-income neighborhoods. In order

to desegregate the student population and make use of the potential peer effects that comes from having

classes with children with various level of abilities, the municipality merged their public secondary

schools into one large school. In the merged school they sort students into mixed classes based on

demographic variables.

Even though this method has been called the ‘the Nyköping model’, merging all public secondary

schools to one is not an initiative unique to Nyköping. From the year of 2012 to 2016 twelve additional

municipalities in Sweden merged their public secondary schools according to the Swedish National

Agency for Education’s SIRIS-database.

The Nyköping model has gotten a lot of attention in media (Svt 2015, Dagens nyheter 2016,

Dagens samhälle 2017). However, it was not until June 2017 that the first student cohort that had the

possibility to attend 7th to 9th grade in the merged school received their final grades. Even though the

effect of the Nyköping model on student outcomes has not yet been extensively studied, there are other

municipalities in Sweden that are considering merging their public schools (Arbetarbladet 2013, Svt

2016).

The aim of this thesis is to examine the effect of the public secondary school mergers on two types

of outcomes. Firstly, I aim to examine whether merging all public secondary schools to one increases

the municipality’s average student academic performance. Secondly, I aim to examine whether a

secondary school merger affects the share of students that attend the public secondary school instead of

choosing to enroll in an independent school.

If the public secondary school mergers have a positive effect on the student’s academic

performance there are incentives for policy makers to encourage the implementation of this type of

initiative. If the mergers have a positive effect on student outcomes, it may be an efficient desegregation

tool. If may also make the public school alternative more competitive. In addition, having just one public

secondary school may be cost-efficient for the municipality.

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On the other hand, the mergers may not be efficient in increasing student achievement. The

municipalities may then end up with schools that accommodate a large number of students. This could

lead to a low teacher density and an impersonal school environment that might not benefit the students.

Bullying and destructive behaviors may not be noted as fast as it could have in a smaller school, and the

within-school segregation between students may not necessarily disappear.

The data that I use is gathered from the Swedish National Agency for Education’s SIRIS database,

which offers aggregate data on municipality-level student outcomes. The time period of this study

stretches from the scholastic year of 2012/2013 to 2016/2017. The time period starts when the first

ninth-grade student cohort received grades according to the 2011 grade reform. The time periods ends

with the most recent available data on 9th grade outcomes.

My identification strategy consists of two methods. My baseline approach is to employ a

difference-in-difference estimation in order to reduce bias from selection on unobservable confounding

factors. I then move on to use propensity score matching to create a control group that potentially

provides a better counterfactual to the treatment group. I use these matches to conduct a difference-in-

difference estimation with match-fixed effects. I find that the results of my baseline approach prove to

be unstable when adding controls to the specification, so I move on to use the matched difference-in-

difference estimation as the main analysis.

I also conduct a heterogeneous treatment effect analysis to explore the potential discrepancy in

treatment effects among students with different backgrounds. The analysis includes comparisons

between female and male students, students of parents with different education levels and students with

Swedish and migrant backgrounds.

Finally, I conduct multiple event studies to examine the validity of the parallel trends assumption.

I also use these studies to examine whether the outcomes are affected by the exposure time of treatment.

My outcome variables are measures on the average student performance of the whole

municipality. Accordingly, the effect that I estimate is the reduced form effect. This reduces the potential

bias from selection in or out of the public-school sector. The reduced form effect holds policy-relevance

since it measures the effect of the school mergers on the average outcomes of the total student population

in the municipality.

My main results show that the public secondary school mergers have a negative effect on the

municipality-level average GPA. The school mergers also have a negative effect on the share of students

in the municipality that pass all subjects and the share that are eligible for a vocational school education.

Thus, the school mergers seem to reduce the share of students in the top of the skill distribution, while

the share of students in the bottom increases. I also use student outcomes from the national standardized

tests as a measure of student academic performance. My analysis shows that the effect of the school

mergers on these outcomes are statistically insignificant and close to zero.

My main results also show that the public secondary school mergers caused the share of 7th graders

enrolled in the public-school sector to decrease by approximately 10 percentage points in the treated

municipalities. This implies that the initiative caused a smaller share of parents to enroll their children

in the merged public schools.

Overall, the public secondary school mergers seem not to be efficient in increasing the

municipality-level student outcomes on average, and it does not seem to improve outcomes for students

in the bottom of the skill distribution. The results indicate that the public secondary school merger is not

a panacea for improving student outcomes.

The remainder of this thesis is organized as follows. Section 2 explains the institutional background

of the Swedish education system and presents previous literature. Section 3 discusses the theory of peer

effects and its importance in the context of this study. Section 4 discusses the data and summary

statistics. Section 5 presents the empirical strategy and underlying assumptions. Section 6 presents the

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main results. Section 7 shows the results of a number of robustness checks. Section 8 includes both a

discussion and concluding remarks.

2. Background

2.1 The Swedish education system

Education in Sweden is compulsory for the first nine years of school, starting at age seven.

Education is offered tuition-free for all levels, which is a Swedish tradition that dates back to the middle

of the 17th century. For long the overall governing of schools and school funding was decided on a

centralized level by the Swedish government and admission to compulsory school was limited to the

students being automatically assigned to the nearest public school in their municipality. Following a

general trend of shifting the responsibility of public service to the municipal level in the 1980s, school

governance was decentralized in 1991. Nevertheless there are still centrally determined curriculums and

goals in each subject that the municipalities are required to meet. This rests on the notion of equal, high-

quality education for all students, independent of which school they attend.

In the fall of 1992, a large voucher reform was introduced which allowed for independent schools

to be established in the municipalities if approved by the Swedish National Agency for Education. Prior

to 1992, students were automatically assigned to the nearest public school in their municipality. The

only alternative was to attend one of the few private schools active in Sweden, however, these schools

were mostly targeting specific demographics of the Swedish population, and less than one percent of

the students attended these schools.

When a student is enrolled in an independent school, the student’s home municipality have to

provide the school with a voucher, equivalent to most of the average per-student expenditure in the

public-school system. The reform allowed students to have the freedom of school choice. This ‘free

choice’ principle allows the student to attend a school outside of his or hers home municipality, and the

voucher will follow with the student to the school. The independent schools are allowed to deviate from

the national standardized curriculum, however they are not allowed to select students for admission

based on ability, socioeconomic background or ethnicity.

The current Swedish grading system is based on a scale of A to F for each subject. This system

came into effect in 2011, but was then only implemented in the 8th grade of compulsory school and in

the 1st grade of upper secondary school, while implementation in the 9th grade was done in 2012. Grades

A to E are passing grades, A being the highest one. The grade F is given when a student has not met the

standard knowledge requirements in the subject. If the student has been absent for too many lessons in

a subject, the school may judge that there is not enough information to assess the student. The school

may then mark the student with a dash (-) instead of a grade in that subject. The dash is not a grade, thus

significantly different from the student receiving an F. The sum of the 16 highest final grades when the

student finishes the ninth year of elementary school is recalculated to a grade point average (GPA).

Receiving an A in a subject yields 20 point. Receiving an F yields 0 points. The final grade GPA ranges

from 10 points to 340 points. A student’s GPA is the basis for admission to upper secondary school.

2.2 Previous literature

In the context of this study, it is interesting to look at literature that examines the effect of school

segregation on student outcomes. Szulkin and Jonsson (2007) examine the effect of ethnic density in

Swedish elementary schools on students’ educational outcomes in ninth grade. They link data on the

ninth-grade student cohorts in 1998 and 1999 with census data on their background characteristics to

establish which students are first and second-generation immigrants. They adopt a multilevel analysis

and find that a high density of first-generation immigrants in a school has a negative effect on a student’s

grade, especially for other first-generation immigrant students. However, a high density of second-

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generation immigrants in a school does not affect the student’s grade negatively. They conclude that

implementing desegregation policies would lead to a reduction in educational achievement gaps

between students.

Nordin (2013) examines whether school segregation affects an individual’s human capital

outcomes. He has access to register data from Statistics Sweden on all individuals aged 20-27 living in

Sweden in 1999. The data also includes information on parental education level and income. Using a

peer effects model with school-fixed effects he estimates the concentration rate of first and second-

generation immigrants in the individual’s school cohort on the outcome variables cognitive ability,

educational attainment and compulsory school grades. In doing so he is able to isolate the within-school

immigration concentration rate which he calls the ‘immigration segregation effect’. He does not find

any significant effects when he include all types of immigrants in his calculations of the immigrant

concentration rate. However, when estimating peer influences of first-generation immigrants and

second-generation immigrants with two foreign born parents, he finds that immigrant peer externalities

have both positive and negative effects on students with immigrant backgrounds. He finds that the peer

effects are sometimes related to lack of Swedish language skills which has a negative effect on students

who also have weak Swedish language skills, while the creation of immigrant peer-groups in schools

has a positive influence on the outcomes for males.

Grönqvist, Niknami and Robling (2015) makes use of a placement policy called the ‘Whole of

Sweden strategy’ to investigate how young males’ criminal behavior is affected by immigrant residential

segregation. The strategy was implemented in Sweden from 1985 to 1994 and meant that the

government was in charge of assigning newly arrived refugees and their families to their initial

residential locations. The authors argue that this should provide exogenous variation to the initial

residential distribution of refugee children. They use population-wide administrative data from 1985 to

2008. The data consists of individual characteristics such as income, educational background and

demographic variables, as well as data on all convictions in criminal trials. This allows them to estimate

the effect of childhood exposure to segregation from the placement policy on long-run criminal

participation. They estimate an OLS that includes a vector of controls for neighborhood characteristics

that vary over time, and municipality-by-year fixed effects. Their dependent variable indicates whether

an individual has been convicted for at least one crime up to the age of 26. Thus their identification

strategy is a linear probability model. Their results show that being assigned to a neighborhood with a

large share of immigrants increases the probability that immigrant males commit drug related offenses

and become incarcerated later in life. They show that these estimates account for a large share of the

native-immigrant crime gap, and that the results are driven mainly by individuals with low educated

parents. The authors conclude that their results provide some evidence that exposure to segregation

during childhood is one of the reasons why young immigrants are overrepresented among criminal

offenders.

Brandén, Birkelund and Szulkin (2016) study how ethnic school segregation in compulsory

schools affects 9th grade students’ educational outcomes. They examine whether attending a segregated

school affects the students’ grade point average and the students’ eligibility for secondary school. To do

this they use Swedish population register data on all students who finished ninth grade between 1998

and 2012. They perform several OLS regressions where they first introduce school fixed effects, then

family fixed effects, and finally a two-way school and family fixed effects design in order to isolate the

‘social-interaction effect’. Thus they try to net out other factors that may affect the student academic

performance such as overall school quality and the potential selection bias that comes from choice of

school. Their estimations show mixed results. Overall, the effect of ethnic segregation on the educational

outcomes is close to zero. Their standard OLS regression shows that grade scores are on average lower

in schools where all students are immigrants than in schools that consist only of native children.

However, the difference between the schools disappears when the school and family fixed effects are

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added. In other words, when the ‘social-interaction effect’ is isolated, the effects perish. In addition,

they find that attending a school with a large proportion of immigrant schoolmates has a small negative

impact on students that are one the margin of not being eligible for upper-secondary schools. Their

conclusion is that ethnic school segregation, if it matters, is mainly affecting students with weak

academic performance. They relate these findings to previous research that shows that skill formation

is crucial in the early years of the child, and that family background has a major influence on the child’s

ability of academic success. From this they conclude that policy interventions trying to change the

composition of immigrants in schools should not affect either immigrant or native children negatively.

Merging all public secondary schools to one in order to decrease segregation and increase student

performance is a type of initiative that is comparable to the desegregation-busing programs that have

been implemented in America since the 1970s. In states with segregated school districts, busing

programs send minority students with low socioeconomic status by school buses to attend schools in

neighborhoods that are predominantly white. There is a large literature that try to estimate the effect of

these types of desegregation programs on student performance and other civic outcomes.

Angrist and Lang (2004) examines the effects of the Metco busing program in Boston. The

program sent black students from Boston schools to attend schools in suburbs outside the city. They use

micro data from the Boston school districts from the year of 1994 to 2000. They estimate the difference

in achievement between Metco-students attending schools in the suburb of Brookline and the resident

students. They find that Metco students had significantly lower test scores than the students that reside

in Brookline. They then move on to estimate the effect of Metco students on the achievement of non-

metco students using both an OLS regression framework and an instrument variables approach where

class size is used as an instrument. They find no statistically significant evidence that Metco students

have any effect on the educational outcomes of their non-Metco classmates. They conclude that peer

effects that arise from the influx of black inner-city students into suburban schools because of the Metco

program are modest.

Johnson (2011) investigates the effect of court-ordered school desegregation programs on

different types of adult socioeconomic and health outcomes. The fact that the court orders were issued

at different points in time creates a quasi-experiment where there is exogenous variation in the

implementation of the programs. Using this variation he estimates a difference-in-difference, a second

least square and a sibling-difference estimation using a panel of children born between 1945 and 1968.

The data includes information on their income until the year of 2013 as well as background

characteristics and school quality measures. His findings show that school desegregation programs

significantly increased educational attainment among black students. Consequently, the accompanied

increases in school quality for black students had a significant positive effect on their labor market and

health outcomes.

Billings et al (2012) study the impacts of the shutdown of a desegregation busing-program in the

Charlotte-Mecklenberg school district in North Carolina in 2002 on academic achievement, educational

attainment and young adult crime. They match university attendance records and incarceration data to

yearly student records from the school district in question. Their identification strategy is to compare

students who live in the same neighborhoods but whose pre-policy addresses placed them on different

sides of a newly drawn school boundary. This caused them to be reassigned to schools with different

racial compositions. They estimate a fixed effects regression and find that both white and minority

students that were reassigned to schools with a higher share of minority students scored lower on their

high school exams. In addition, the policy change widened the performance gap between black and

white students. However, for primary school students the negative impact was smaller. Overall the

effects of the minority-student influx to schools on student achievement diminished over time. An

increase of the share of minority peers increased the probability that minority males take part in criminal

activity, which stayed persistent over the years. The authors conclude that the diminishing impact on

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student achievement was due to compensatory allocation of resources to the schools, while the impacts

on crime seemed not to be affected by increasing school resources.

3. Theory

When changing the school organization within a municipality in the way as Nyköping has done,

one changes the composition of the school cohorts, mixing students together in order to reduce

segregation among the youth population and increase student performance. The term peer effects in the

education of economics literature is defined as the externalities that comes from peers in the classroom

or in the general school environment affecting the outcome of another student. A problem is that peer

groups are often created endogenously. This may be optimal for the students that choose the ‘right’ type

of peers since it optimize their outcome. However, their actions may not optimize the social outcome.

Consequently, there are opportunities for school officials to create incentives for students to interact

with the socially optimal distribution of peers within the school (Hoxby 2000).

Manski (1993) divides peer effects into three different types. The first one is when the peers’ own

abilities affect another student’s outcome. The second one is when the peers’ background characteristics

affect another student’s outcome. This may affect the student’s outcome directly in class and indirectly

through the level of difficulty that the teachers adopt in the classrooms or the peers’ parent’s impact on

school decisions. The third type is the correlated peer effects. These arise when students spend a lot of

time together in the same institutional setting. In this setting, a school for instance, they are treated by

common shocks. This may be that they are taught by the same teachers or influenced by the same type

of social norms which will cause them to adopt similar traits that in turn will affect their outcomes.

A basic model of the effects of peers on a student’s outcome is a linear-in-means estimation,

assuming that only the first two types of peer effects affect the outcome of the student:

𝑌𝑖 = 𝑎 + 𝛽1 ∗ �̅�−𝑖 + 𝛾1 ∗ 𝑋𝑖 + 𝛾2 ∗ �̅�−𝑖 + 𝜀𝑖 (1)

𝑌𝑖 is student i’s outcome, for instance the student’s performance in school. �̅�−𝑖 is the peers’ average

outcomes, which may be interpreted as the peer’s average performance in school, affecting student i’s

outcome if 𝛽𝑖 ≠ 0. 𝑋𝑖 is a vector of student i’s own background characteristics. �̅�−𝑖 is a vector of the

peers’ background characteristics, affecting student i’s outcome if 𝛾2 ≠ 0. 𝜀𝑖 is the error term.

Several problems arise when economists try to empirically estimate peer effects. One problem is

the reflection problem (Manski 1993), that arises from the fact that student i is a peer of her classmates.

Hence the student’s outcome 𝑌𝑖 will affect her peer’s outcome �̅�−𝑖 which introduces simultaneous

causality to the linear model.

A second problem is the self-selection into peer groups based on unobserved factors. For example,

even though sorting into a group may be done in part based on observables such as background

characteristics, the peers may self-select into sub-groups in ways that unobservable (Sacerdote 2001;

Carell et al 2011). This means that the third peer effect, the correlated effect, is not observable in the

data but still affects 𝑌𝑖, which will lead to bias estimates.

A third problem is the difficulty to establish whether it is the peers’ abilities or background

characteristics that have a causal effect on the student’s outcomes. The peers’ abilities are in themselves

affected by their backgrounds. Consequently, even if one may assume that the effects of peers’

background characteristics have a causal effect on the student outcomes, it may not be possible to

separately identify 𝛽1 and 𝛾2.

Because of these problems, most economists employ an estimation of the reduced form effect of

peer effects (Sacerdote 2001; Angrist and Lang 2004; Carell et al 2008; Carell et al 2011).

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In this study I will not be able to establish the effects of peers on the students’ academic outcomes

within the merged schools. This is because I work with aggregate data and cannot make inferences about

the actual students in the classrooms. However, the underlying mechanisms of peer effects may explain

the motivational reasons for why municipalities merge their public secondary schools.

Firstly, the most prominent goal of the public secondary school merger in Nyköping is to reduce

segregation among its youth population. In essence, what Nyköping is hoping for is an ‘integration

effect’ where a student population with diverse backgrounds will create positive peer effects that in turn

will increase the student’s academic performance. However, under the assumption that peers affects

outcomes as in the linear model specified in equation (1), sorting students into mixed classes should not

have any effect on average student performance. This is because the positive effects that the group of

low-ability students experience will be net out by the negative effects that the group of high-ability

students will encounter.

We can relax the linearity assumption and assume that weak students experience positive effects

from high-ability peers, while high-ability peers are not hurt by having low-ability school mates. What

we could expect in this case is that the average student performance should increase when students with

diverse backgrounds and abilities attend the same schools. The positive effects of the public secondary

school mergers on average student academic performance hinges on the belief that peers will affect each

other in this ‘non-linear’ manner. This is why school officials believe in sorting the classes on

demographic variables as a way to optimize the distribution of peers in each classroom. On the other

hand, the students may create sub-groups within each class, and still interact with the students that they

would have attended the same school with if the merger had not been implemented.

The officials may believe that the students with high socioeconomic status will perform just as

well in the merged school as they would have if they attended a school close to their home. This should

have a positive influence on students with low socioeconomic status. This means that the presence of

students with high socioeconomic status will cause 𝛽1 > 0 for their classmates. However, students with

high socioeconomic status may have done well in their old school because they were in a homogeneous

environment and only associated with other students of high socioeconomic status. In essence, the

potentially positive peer effects from this group may not be as positive as the officials hope for. In this

case, the ‘integration effect’ may be smaller than predicted.

Secondly, one may assume that good-quality teachers choose employment at schools where

student’s average performance is high. Students in the merged school who otherwise would have gone

to a school where the average student performance was low may now have teachers of greater quality

because their peers will attract them to seek employment at the new school. However, it might also be

the case that teachers who otherwise would have taught students with high socioeconomic status is

biased towards students with low socioeconomic status. These students may then not get the resources

that they need to increase their academic performance.

Finally, when the school mergers are implemented, parents who are about to make the choice of

school for their child will essentially choose the one public school available or an independent school

alternative. If the peer effects that comes from attending the merged schools are linear, then children

with low ability will benefit from attending the merged school. However, children with a high

probability of scholarly success will be on the downside of the initiative. Students with low

socioeconomic status or immigrant background might benefit from learning in a heterogeneous school

environment, while students with high socioeconomic status or native background might benefit from

attending a school with peers that are similar to themselves. In this case the parents of these children

might choose to enroll their children in an independent school as a reaction to the school mergers. The

result may be that the school mergers actually cause school segregation to increase in the municipality

rather than to eliminate it.

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4. Data

4.1 Data description and coding issues

This study aims to examine in which ways the public secondary school mergers affect student

outcomes. The data is gathered from the Swedish National Agency for Education’s SIRIS database,

which offers municipality or school level data on the Swedish education system. The database is built

on individual-level data that Statistics Sweden gathers by order of the agency.

The time period of this study stretches from the scholastic year of 2012/2013 to 2016/2017. The

9th grade student’s academic outcomes are recorded in the end of each scholastic year. The most recent

available data is from the scholastic year of 2016/2017. As mentioned in section 2.1, the grade reform

of 2011 did not affect the 9th graders until the scholastic year of 2012/2013. The reform entailed that an

entirely new grade system was implemented. Because of this, the aggregated data on test and grade

results provided by SIRIS is considerably different before and after the reform. In order for the grades

and test results to be comparable between the student cohorts, my panel does not stretch further back

than to the year of 2012/2013.

The SIRIS database also offers data on municipality-level student characteristics for the entire

compulsory school population (grades 1-9). I use these variables as controls for municipality

demographics. The controls that I include are the share of female students, the share of students with

migrant background and the share of student with parents that have a university education. Students

with migrant background are defined as students with both parents born outside of Sweden. Students

with parents who have a university education is defined as students who have at least one parent who

attended university.

The data includes municipality-level outcomes and control variables for all municipalities in

Sweden. Some values in the SIRIS raw data are coded as missing instead of its real values due to

different reasons. I will briefly go through how I have handled these coding issues.

Firstly, the raw data includes some missing values for some municipalities some years. This data

is coded as (.) in SIRIS. It is probable that this issue rises due to the fact that it is formally the official

for each school that is responsible to provide Statistics Sweden with the data material. For the public

schools this is done by the municipality officials. For the independent schools it is either the headmaster

or the company that runs it that is responsible. Neither Statistics Sweden nor the Swedish National

Agency for Education holds the main responsibility, and it is therefore believable that some outcomes

are missing due the human error. When the outcomes are missing for a specific municipality for two

years or less, I use interpolation. However, when a municipality have missing values for the majority of

the years it has been omitted.

Secondly, there are some values that are coded as ~100 in the ‘share outcomes’ data, for example

the share of students that pass the national standardized tests. When there are four students or less that

fail the test, the share of students that pass are coded as ~100. There is no real clarification on SIRIS on

what ~100 actually means, but it could be interpreted that ‘approximately 100 percent’ of the students

passed. Note that this is not the true value of the outcome. We can assume that the true value will move

towards 100 percent when the student population is large. However, if the student population is small

the true value will not be approximately 100.1 I have no way of knowing the true value of these

outcomes. I have solved this coding issue by creating two different types of measures for these outcome

variables. For the first type of outcome variable I assume that four students failed to pass (the ‘worst

case’ scenario) and then calculate the true value of this case by dividing four by the student population

1 A municipality with a student population of a thousand students where four students fail to pass the national standardized test

will have a 99.6 percent share that did. However, a municipality with a student population of twenty students where four

students failed to pass, will have an 80 percent share that passed. Recoding the ~100 value to 100 for this municipality is not

close to the true value of the share that passed.

- 9 -

and subtracting it from 1. In this ‘worst case’ variable the ~100 values are recoded with the value of my

calculations. I also create a variable where all the ~100 values are recoded as 100, a ‘best case’ scenario.

I will use the ‘worst case’ outcome variables in my analysis. This is because it is likely that at least some

students should fail to pass in each municipality and using the ‘worst case’ scenario accounts for this.

This issue will be further discussed in section 7.4.

Finally, when the outcome is based on ten students or less, the outcome is coded as (..) instead of

its real value. This may be considered fair on the basis of anonymity in the Swedish Personal Data Act,

but it poses somewhat of an issue for statistical inference since it produces missing values that are never

random.2 I treat these values as missing and either use interpolation to get an estimated value or omit

the municipality.3

I have created seven panels for the different types of outcomes used in this study. In each panel

I assess which municipalities that needs to be omitted. Because of this most of the samples differ in size.

Accordingly, the results of each panel need to be analyzed separately. The panel datasets I have

constructed for the main analysis are:

Main analysis panels:

Panel 1 - Final grade outcomes

Panel 2 – Share of students in a municipality’s public schools

Panel 3 - National standardized test outcomes

Panels 1-3 is used for estimating the overall effects of the school mergers. However, the results

may conceal adverse effects for certain student groups. There may be substantial variation in how

students respond to treatment because of their background characteristics. Initiatives to decrease school

segregation aims to target groups of students that are disadvantaged. It is interesting to explore potential

discrepancy in treatment effects among different student groups. I have obtained data on student

outcomes divided on certain characteristics and created the following panels:

Heterogeneous treatment effects analysis panels:

Panel 4 – final grade outcomes divided on gender

Panel 5 – final grade outcomes divided on parental education level

Panel 6 – final grade outcomes divided on Swedish and migrant background

There are some notes to make on the heterogeneous treatment effect panels. In panel 5 the final

grade outcomes are reported for two student populations divided on parental education level. The first

group is ‘students of parents with a upper-secondary school education’, which includes students for

which the highest level of education that both parents have is either a secondary school or upper-

secondary school education. The second group is ‘students of parents with a university education’,

which includes students who have at least one of the parents attended university. Panel 5 differs

considerably from the other panels as it only includes the time period 2014/2015-2016/2017.4

2 I am sometimes able to calculate the real value of (..) for the number of students of in a certain student population when I

have the real value of the number of total population and the real value of the number of students in the other student population.

I cannot calculate the true value of any of the outcome variables since it needs to be calculated using individual data that I do

not have access to. 3 The data for some municipalities may not have any (..) values for outcome measures based on the total ninth-grade student

population, but it may need to be omitted from the panel when the outcomes are divided on student background characteristics. 4 The group “students of parents with an upper-secondary education” did not include students of parents who just had a

secondary school education before the scholastic year of 2014/2015. Instead, these students were included in their own group

in the SIRIS data. In the raw data it was not possible to recalculate the outcome measures for the three groups in 2012/2013-

2013/2014 in order to make the measures comparable with the two groups reported after 2014.

- 10 -

In panel 6 the final grade outcomes are reported for two student populations that are divided on

Swedish and migrant background. The first group is ‘students with Swedish background’, which

includes students born in Sweden with at least one parent born in Sweden. The second group is ‘students

with migrant background’, which includes students born outside of Sweden who have migrated to

Sweden with their families.5

4.2 Outcome variables

This study focuses on the effect of the secondary public-school mergers on two different types of

outcomes. Firstly, I want to investigate the effect on the municipality-level 9th grade student academic

performance. To do so I look at the final grade outcomes and national standardized test results. The final

grades that the students receive in the end of ninth grade constitute the ground for admission to upper-

secondary school. The purpose of the national standardized tests is mainly to provide teachers across

the country with the same basis for grade assessment. The tests are marked and graded according to

national guidelines.

There are some differences between the two measures for the students’ academic performance.

The final grades are based not only on the student’s result on the national standardized test, but also the

student’s overall performance in 7th to 9th grade. Hence, the result that the student gets on the national

standardized test does not need to be equivalent to the final grade that the student receives. In this sense

treatment may have different effects on these two outcomes. I therefore analyze both. In detail, the

outcome variables that measure student academic performance are:

(i) average final grade GPA

- The municipality-level average GPA. This outcome may be seen as a measure for the

average performance of the total student population. Only students who passed 9th grade

is included in the data. Hence in my panels the highest GPA value is 340 while the

lowest is 10.

(ii) The share of students that passed all subjects in ninth grade

- The municipality-level share of students that did not receive any (F) or (-) grading. This

outcome may be seen as a measure that captures the effect of treatment on students in

the top of the student skill distribution.

(iii) The share of students eligible for a vocational education

- To be eligible for a university prepatory program in upper secondary school a student

has to pass twelve out of seventeen subjects. In total the student needs to pass eight

subjects to become eligible for admission at a vocational school program. This outcome

may be seen as a measure that captures the effect of treatment on students in the bottom

of the student skill distribution.

5 SIRIS have data on a third student population distinction; students who are born in Sweden with both parents born outside

of Sweden. Including this group caused the data to contain missing values for a large portion of the municipalities due to the

issue with the (..) coding. This meant that almost all treatment municipalities would have needed to be excluded. Therefore, I

do not include this student group in my study.

- 11 -

(iv) Average national standardized test GPA (in English, math, Swedish)

- The municipality-level average test GPA. The grading on the test is recalculated into

points. Receiving an A in a subject yields 20 point. Receiving an F yields 0 points. All

students who participated are included in the data. Thus, the average test GPA varies

between 20 and 0.

(v) The share of students who passed the national standardized test (in English, math, Swedish)

- A measure for the municipality-level share of students who received grades A-E on the

tests out of all students who participated (received A-F).

Secondly, I want to examine the effect of the public secondary school mergers has on the student’s

choice of enrolling in a public school instead of choosing an independent school alternative. The

outcome variable for the effect of the school mergers on share of students in the public-school sector is:

(vi) The share of 7th grade students enrolled in public school in a municipality

- The value is calculated by taking the number of 7th graders enrolled in the public schools

and divide it by the total number of 7th graders in each municipality each year.

The reason why I examine the behavior of 7th graders is because it is common in Sweden to divide

grades 1-3, 4-6 and 7-9 into different schools (Swedish Agency for Education, 2017). In this case, the

parents have to choose a new school for the child between the 6th and 7th grade. The parents then have

the opportunity to choose an independent school option instead of a public one, and vice versa. The

merged schools that are included in this school include grades 7 to 9. Using the share of 9th graders may

be considered fruitless due to the fact that students and parents may be hesitant towards switching

schools right before the last year of secondary school.

4.3 Treatment and control groups

According to the SIRIS database there are twelve municipalities that have implemented the

merger during the time period of my study. These municipalities are presented in table 1. Column (2)

shows the scholastic year that the merged secondary public school opened, and column (3) shows the

name of the new school. The number of students in the scholastic year of 2016/2017 is shown in column

(4). In 2016 the average number of students in public secondary schools in Sweden was 217 students

(Swedish agency of Education, 2017). All of the merged schools have a larger body of students than the

national mean. The two largest schools reside in Katrineholm and Nyköping, where the student

population consists of over 1000 students.

For the six panels that I use in this study the treatment group differs in size. This is due to the

various nature of the outcome variables. The municipalities included in each treatment group are

presented in table 2.

When I estimate the effect of the secondary school mergers on student academic achievement the

requirement for a municipality to be included in the treatment group is that the merged school have been

opened for at least three years. As noted earlier, the merged school in Nyköping opened in 2014/2015.

This implies that the ninth-grade student cohort in the scholastic year of 2016/2017 was the first cohort

that had the possibility to attend the merged school throughout 7th to 9th grade. It would be optimal to be

completely certain that the student cohort did attend the merged school during these years in order to

eliminate the effect that attending another school may have on the students’ ninth-grade outcomes. Since

- 12 -

I only have access to municipality-level data I cannot be certain of this. Nevertheless, it is possible that

a small number of student switched schools sometime between 7th and 9th grade.6

Table 1. Treatment municipalities (1) (2) (3) (4) (5)

Official

mun.

key

Scholastic year

of

school merger

Name of

secondary school

Number of

students

(2016)

Independent

schools in

municipality

Flen 0483 2015/2016 Stenhammarskolan 427 No

Götene 1471 2015/2016 Liljestensskolan 464 No

Hedemora 2083 2013/2014 Vasaskolan 419 Yes

Katrineholm 0483 2016/2017 Järvenskolan 1,055 Yes

Lilla Edet 1462 2015/2016 Fuxernaskolan 136 Yes

Munkedal 1430 2013/2014 Kungsmarksskolan 343 No

Nyköping 0480 2014/2015 Nyköpings högstadium 1,261 Yes

Skara 1495 2015/2016 Viktoriaskolan 557 Yes

Surahammar 1907 2013/2014 Hammarskolan 320 No

Säffle 1785 2015/2016 Tegnérskolan 524 No

Årjäng 1765 2015/2016 Nordmarkens skola 349 No

Älmhult 0765 2014/2015 Linnéskolan 433 Yes

Örkelljunga 1257 2013/2014 Kungsskolan 271 Yes

The data is gathered from the Swedish National Agency for Education’s SIRIS database. The official municipality

keys in column (1) are identification numbers provided by the Swedish Tax Agency. The number of students for

each school as shown in column (4) is the number of students that are enrolled in each school on the 15th of October

2016.

As shown in table 2, the treatment group that I use when I examine the effect of the school mergers

on the students’ academic outcomes only includes municipalities that implemented the merger in 2014

or earlier. This is to make sure that the students have had the possibility to attend the merged school

from 7th to 9th grade. These municipalities are; Hedemora, Nyköping, Surahammar, Älmhult,

Örkelljunga and Munkedal.

In column (5) we see that the municipalities in the treatment group when the final grade outcomes

are divided on parental education level differ as it includes; Flen, Götene, Skara, Säffle, Årjäng and Lilla

Edet. These municipalities are the ones where the merged schools opened in the fall of 2015.7

In column (6) we see that there are only three municipalities included in the treatment group when

the final grade outcomes are divided on students with Swedish and migrant backgrounds. This is due to

the fact that the outcome data divided on Swedish and migrant background includes many missing

values and in affect some of the treatment municipalities needed to be excluded from the data. The

municipalities included in the treatment group in this panel are; Hedemora, Nyköping and Älmhult.

When I estimate the effect of the school mergers on the share of students in the public-school

sector, I impose another requirement on the municipalities that are included in the treatment group. The

requirement is that there actually exist independent schools in the municipality. In column (5) of table

1 we see that not all municipalities do. The students in these municipalities does not have the option of

6 This would be if they switched from an independent school or moved in to the municipality. In contrast to public schools,

independent schools do not have to admit all applicants each year, and there is usually a queuing system. The independent

schools may presumably be reluctant to admit students when their classes are already filled according to the que. 7 As explained in the previous section this panel only include the time-period of 2014/2015-2016/2017. In this case the

constraint that schools have to been open for at least three years needs to be loosened. Thus, these schools have been opened

for two years, which means that the 2016/2017 9th grade student cohort only had the opportunity to attend the school in 8th

grade too.

- 13 -

attending an independent school. I do not include thee municipalities in the treatment group.8 As shown

in table 2, column (2), the municipalities included in this treatment group are; Hedemora, Nyköping,

Skara, Älmhult, Örkelljunga and Lilla Edet.

The control group consists of all municipalities in Sweden that had a constant number of public

secondary schools during the time-period of this study. The municipalities that experienced an increase

in the number of public schools during the time-period of this study are excluded. There are also a

number of municipalities that had a decreasing number of public schools during this time. These

municipalities are also excluded. In total 48 municipalities are excluded from all panels.9

Table 2. Municipalities in treatment groups

Municipalities included in treatment group for different panels

(1) (2) (3) (4) (5) (6)

Panel 1:

Grade

outcomes

Panel 2:

share 7th grade

students in public

schools

Panel 3:

National

standardized

test

Panel 4:

Grade

outcomes div.

on gender

Panel 5:

Grade outcomes div.

on parental

education-level

Panel 6:

grade outcomes div.

on background

Flen No No No No Yes No

Götene No No No No Yes No

Hedemora Yes Yes Yes Yes No Yes

Katrineholm No No No No No No

Lilla Edet No Yes No No No No

Munkedal Yes No Yes Yes No No

Nyköping Yes Yes Yes Yes No Yes

Skara No Yes No No Yes No

Surahammar Yes No Yes Yes No No

Säffle No No No No Yes No

Årjäng No No No No Yes No

Älmhult Yes Yes Yes Yes No Yes

Örkelljunga Yes Yes Yes Yes No No

This table shows which municipalities are included in the treatment group. Columns (1)-(3) presents the treatment groups used

in the main analysis. Columns (4)-(6) shows the treatment groups used in the heterogeneous treatment effects analysis.

8 None of the treated municipalities had an independent school that opened during the time period of this study. 9 The names and official municipality keys of these municipalities are shown in table A1 in appendix A.

- 14 -

4.4 Descriptive statistics

Table 3 shows summary statistics for each panel that is used in the main analysis. ‘Panel 1 - final

grade outcomes’ includes 235 municipalities over the five-year period of this study. The treatment group

consist of six municipalities, while the control group consists of 229 municipalities. Overall the mean

outcomes are slightly larger for the control group than for the treatment group. The largest difference is

the mean number of ninth-graders in the municipality. Note that this variable includes the total ninth

grade student population in a municipality, thus it includes students in both the public and independent

school sector. The difference is probably due to the fact that the control group includes some

metropolitan municipalities with large student populations while the treatment group includes almost

only small and rural municipalities. ‘Panel 2 – share of students in a municipality’s schools’ includes 93

municipalities, for which six constitutes the treatment group and the remaining 87 municipalities the

control group. The share of 7th graders that are enrolled in the public-school sector in each municipality

is the outcome variable, the mean share in the total student population is 78.5 percent, and the mean in

treatment and control group does not deviate much from this. The average size of the municipality-level

student population differs considerably between control and treatment group. The municipality-level

mean number of students in 7th grade the control group is 2279 students, while in the treatment group

the mean number of 7th graders is 361 students. The difference is also large when comparing the mean

number of 7th graders in the public-school sector and independent school sector. ‘Panel 3 – standardized

national test outcomes’ for the total student population consists of 232 municipalities out of which six

municipalities received treatment. The table shows that there are no considerable differences in mean

outcomes between treatment and control group.

- 15 -

Table 3. Summary statistics for final grade outcomes and share of students in a municipality All municipalities Control municipalities Treated municipalities

(1) (2) (3) (4) (5) (6) (7) (8) (9) (10)

N n mean sd n mean sd n mean sd

Panel 1: grade outcomes

Average GPA 1,175 235 219.8 15.35 229 219.9 15.39 6 211.1 8.715

Pass all subjects (%) 1,175 235 76.58 7.110 229 76.64 7.105 6 72.07 6.057

Eligible voc. school (%) 1,175 235 85.82 5.634 229 85.86 5.633 6 82.68 4.901

No. 9th grade students 1,175 235 1583 2653 229 1599 2666 6 335.0 240.7

Female students (%) 1,175 235 48.51 1.095 229 48.50 1.091 6 48.97 1.309

Immigrant background (%) 1,175 235 20.39 10.06 229 20.41 10.11 6 18.99 4.468

Students of parents with

university education (%)

1,175 235 53.35 10.76 229 53.46 10.76 6 45.06 6.902

Panel 2: share of students

in mun. pub. schools

7th grade students Pub. (%) 464 93 78.48 11.62 87 78.53 11.65 6 75.75 9.342

No. 7th grade students tot. 464 93 2247 3131 87 2279 3148 6 360.9 230.7

No. 7th grade students Pub. 464 93 1516 1917 87 1538 1926 6 256.6 145.1

No. 7th grade students Ind. 464 93 721.6 1208 87 732.1 1216 6 104.3 87.39

Female students (%) 464 93 48.62 0.840 87 48.62 0.831 6 49.16 1.190

Immigrant background (%) 464 93 21.89 10.47 87 21.91 10.54 6 20.73 4.295

Students of parents with

university education (%)

464 93 57.28 9.305 87 57.48 9.218 6 45.68 6.929

Panel 3: national test

English test:

Average grade point 1,155 231 14.44 0.839 225 14.44 0.844 6 14.42 0.529

Share pass test 1,155 231 95.15 2.987 225 95.15 2.991 6 95.34 2.852

Math test:

Average grade point 1,155 231 10.92 1.382 225 10.92 1.390 6 10.81 0.930

Share pass test 1,155 231 84.65 8.302 225 84.67 8.329 6 83.74 6.847

Swedish test:

Average grade point 1,155 231 12.99 0.967 225 12.99 0.970 6 12.82 0.798

Share pass test 1,155 231 94.01 3.796 225 94.01 3.809 6 94.31 3.134

Control variables: 1,155 231 12.99 0.967 225 12.99 0.970 6 12.82 0.798

Female student (%)

Immigrant background (%) 1,155 231 48.31 1.658 225 48.30 1.660 6 48.86 1.457

Students of parents with

university education (%)

1,155 231 16.57 7.849 225 16.53 7.890 6 18.18 5.142

No. 9th grade students 1,155 231 45.93 10.18 225 46.02 10.23 6 41.32 5.931

The data is gathered from the Swedish National Agency for Education’s SIRIS database. All summary statistics are based on

the scholastic years of 2012/2013-2016/2017. N shows the number of observations in the total dataset, while n shows the

number of municipalities.

- 16 -

5. Method

5.1 Empirical framework

This study aims to examine the effect of the secondary school mergers on the municipality-level

student outcomes. Treatment occurs when the municipality goes from having several public secondary

schools to have one school. When estimating this type of treatment effect, there may be unobservable

factors correlated with treatment and affecting the outcome that vary between municipalities or over

time. In order to isolate the effect of the secondary school mergers and reduce bias from selection on

unobservable factors, I employ a difference-in-differences estimation as my baseline approach. Thus, I

compare the change in outcome in municipality that has been subject to treatment with change in

outcome in untreated municipalities over time. My baseline estimation is the following:

𝑌𝑚𝑡 = 𝛼 + 𝛽𝑇𝑚𝑡 + 𝛾𝑋𝑚𝑡 + 𝜃𝑚 + 𝜆𝑡 + 𝜀𝑚𝑡 (2)

𝑌𝑚𝑡 denotes the average student outcome in the municipality. 𝑇𝑚𝑡 is a dummy variable taking on

the value one if a municipality that is exposed to treatment is in a period where it receives treatment.

Hence, 𝑇𝑚𝑡 equals zero if a treated municipality is in a pre-treatment period or if the municipality is in

the control group. Accordingly, 𝛽 is the difference-in-difference estimator which is the parameter of

interest. 𝑋𝑚𝑡 is a vector that includes controls for the municipality demographics. 𝜃𝑚 denotes the

municipality-fixed effects. This eliminates bias arising from there being unobservable factors that vary

across municipalities but are constant over time. 𝜆𝑡 denotes the time-fixed effects. This eliminates bias

arising from unobservable factors that are constant across municipalities but vary over time. All

municipalities are weighted on their 9th grade student population in order to correct for differences in

population size.

Considering the fact that I study the effect of the public secondary school mergers on student

outcomes for the entire municipality, what I estimate is essentially a reduced-form effect. Thus, the

difference-in-difference estimator captures the overall impact of the initiative on the municipality’s

student performance or choice of school. By using outcome data for the entire municipality I reduce the

risk of ‘selection into treatment’ within the municipality. The selection problem could arise if the

students that attend public schools do so because they have certain background characteristics that

makes them different form students that attend independent schools. By estimating the effect of the

initiative on the municipality-level student outcomes I am able to see how the opening of the merged

school is affecting the overall performance of the municipality’s student population, which could capture

any potential spillover effects from the initiative on students who attend independent schools in the

municipality.

In this study the standard errors are clustered on municipality-level to allow for the residuals

within municipalities to be correlated. In other words, I allow for the error term to be correlated within

a certain cluster of entities, yet uncorrelated across clusters. Donald and Lang (2007) point out that the

estimator of the standard error is only asymptotically consistent when the number of observations in the

treatment and control groups are large. The fact that the time-period of this study is only five years long

may cause the standard errors to be inconsistent.

According to Conley and Tabler (2011) having a large sample might not always cause the standard

errors to be consistent if the number of treated observations is small. They argue that in this case,

assuming that the standard error estimates are asymptotically normally distributed may not be

appropriate. They a framework for the estimation of the standard errors that causes them to be consistent

when the treatment group is small. Their strategy is to create an empirical distribution of the residuals

from control group. This creates an asymptotically valid acceptance region for the null hypothesis that

the difference-in-difference approach estimates the true causal effect. If the estimates lie in the tails of

the empirical distribution, the null hypothesis can be rejected. The key idea is that although the control

- 17 -

group does not provide any information about the true value of the difference-in-difference estimator, it

can contain information about the distribution of the noise in the error term. If the number of

observations in the control group is large one could be able to make a consistent estimation of the

distribution of the point estimators up to the true value of the causal effect.

I will use the municipality-level clustered standard errors throughout this study under the

assumption that they are consistent, however this issue is worth noting since the number of

municipalities in the treatment group in the panels are at the most six. The method that Conley and

Tabler introduce would be a useful technique to use in a possible extension of the framework I employ

for my analysis. However it is outside the scope and time frame of this thesis in its current form.

5.2 Underlying assumption

The key identifying assumption is that aside of the secondary school merger, there are no

unobservable confounding factors that vary both over time and across municipalities systematically

affecting student outcomes in the treated municipalities. This essentially means that one would be able

to observe the same trends in changes of potential student outcomes for both treatment and control

municipalities over time if treatment had not occurred. It is important to note that these trend-changes

are not observable. This is because they refer to trends in outcomes in an alternative world where the

secondary school mergers would not have occurred in the municipalities. Looking at what the

difference-in-difference estimator is actually measuring may bring clarity to this issue. The difference-

in-difference estimator, given by 𝛽 in this study, compares the change in student outcomes before and

after the mergers have been implemented in the municipalities to the changes in student outcomes for

the same time periods in municipalities where no school mergers occurred. Thus, the estimator is given

by:

𝛽 = [𝐸(𝑌𝑡1|𝑚𝑇) − 𝐸(𝑌𝑡−1

0 |𝑚𝑇)] − [𝐸(𝑌𝑡0|𝑚𝐶) − 𝐸(𝑌𝑡−1

0 |𝑚𝐶)] (3)

In equation (3), 𝑌𝑡1 is the expected outcome of treatment municipality 𝑚𝑇 in period t which is

when treatment occurs. This makes it clear that the difference-in-difference estimator compares changes

in expected outcomes between treatment and control group.

The parallel trends condition says that if treatment never had occurred the changes in expected

outcomes will be equal between treatment and control group. Hence, this is in the alternative world

where 𝑌𝑡1 never happens. Therefore, this scenario can be shown as:

𝐸(𝑌𝑡0|𝑚𝑇) − 𝐸(𝑌𝑡−1

0 |𝑚𝑇) = 𝐸(𝑌𝑡0|𝑚𝐶) − 𝐸(𝑌𝑡−1

0 |𝑚𝐶) (4)

Equation (4) essentially tells us that if treatment never had occurred, one would have been able to

observe the same trends in potential student outcomes for the municipalities in the treatment and control

group over time.

As noted earlier we are not able to observe the alternative universe where the merger was never

implemented in the municipalities in question. However, it is possible to test the assumption by

conducting placebo tests on pre-treatment periods. Thus, the procedure of the parallel-trends test is to

estimate the effect of treatment on the sample in the period before treatment actually happened. This

requires that one have access to data on multiple years before the merger to be able to look at

pretreatment trends. I do not have access to enough pre-treatment data to observe any trends, but there

are some municipalities that have two pre-treatment periods.

In order to observe the parallel trends one need to look at the pre-treatment trends over time, and

therefore it is not enough to only have one pre-treatment period. Since I do not have enough pre-

- 18 -

treatment periods I cannot perform a placebo test that is representative for the entire treatment group. I

am however able to explore whether the parallel trends assumption holds for the municipalities in the

treatment group that have more than one pre-treatment period by conducting a number of event studies.

In these event studies I plot the difference-in-difference point estimates where the binary treatment

variable has been interacted with the years before and after the public secondary school mergers where

implemented. The results of these tests will be further discussed in 7.1.

There are two reasons why an insignificant point estimate in year t-2 may still not be valid

indicator that the parallel trends assumption holds. Firstly, the effect in year t-2 is only calculated based

on the municipality that have two pre-treatment periods, and therefore the point estimate does not reflect

the whole treatment group. Secondly, since I am only able to observe the point estimate for one pre-

treatment period, and it may therefore not say much about the parallel trends over time.

5.3 Matching

The difference-in-difference approach compares the trend in average outcome between treatment

and control group. Essentially, I estimate the trends in average outcome for the control group and uses

it as a proxy for the counterfactual outcome. How to find a suitable control group depends on the

assignment mechanism. If the school mergers are implemented randomly in the municipalities in

question, then on average the estimation of trends in potential outcomes between treatment and control

group should provide unbiased estimates. However, if there is self-selection into treatment based on

trends in deteriorating school performance or demographics that caused the municipalities to implement

the school merger, then non-treated and treated municipalities may have very different potential

outcomes settings, which would cause biased estimates.

In order to create a control group that potentially provide a more suitable counterfactual I want

to explore the alternative of restricting the control group. To do so I use propensity score matching to

create new panels that contain the treatment group and a control group that is more similar on

municipality demographics. In the matching process each treated municipality is matched to the

untreated municipality with the closest propensity scores. The propensity score is the probability that a

municipality receives treatment given the observable confounding factors.

The matching is done on a set of pre-treatment covariates10. Ideally one wants to perform the

matching on pre-treatment trends, however due to the small number of pre-treatment periods available

to me I use the level of the covariates. Most of the panels used in this study has a staggered treatment.

Therefore, some of the treated municipalities have two pre-treatment periods while others just have one.

In order to have the same number of nearest neighbors for all treatment municipalities within each panel,

the matching had to be done on covariates from the same pre-treatment period for the entire treatment

group. Because of this, the matching is done on covariates from the scholastic year of 2014/2015 for the

panel where the final grade outcomes divided on parental education level, and 2012/2013 for all the

other panels.

As mentioned in the previous section the number of treated municipalities is small. I therefore use

M-nearest neighbor matching with redraw so that each treated municipality gets several control group

matches in order to not lose too many observations in the control group.11 I match each municipality in

10 The covariates that are used in the matching process for the student performance outcome panels: final grade or national

standardized test outcomes, the mean number of ninth-graders in the municipality, the number of the total compulsory school

student population (grades 1-9), the share of 9th grade students enrolled in the public-school sector, and the control variables

(see section 4.1). The pre-treatment covariates that are used in the matching process for the share of students in a municipalities

public schools: the share of 7th graders in the public-school sector, the number of 7th grade students in the public and

independent school sector, the mean number of students enrolled in 7th grade, the number of the total compulsory school student

population (grades 1-9), the share of 9th graders enrolled in the public-school sector, and the control variables (see section 4.1). 11 Selecting the number of neighbors to match on involves a bias called variance trade-off (Stuart 2010). Matching each

observation with a larger number of neighbors may decrease variance due to a larger sample size. On the other hand, including

- 19 -

the treatment group with the five untreated municipalities that have the closest propensity score. Due to

the fact that the treatment group in ‘Panel 6 – final grade outcomes divided on Swedish and migrant

background’ have less than five municipalities in the treatment group due to reasons discussed in section

4.3, the treated municipalities in this panel is matched with the three closest m-neighbors.12

The propensity score matching is done in several steps. First, I need to change the dimension of

the panel data from long to wide to treat all covariates each year as cross-sectional data. I then estimate

the propensity score using a logit model given the pre-treatment covariates. Based on the propensity

score I match the treated municipality with the untreated municipalities that have the closest scores. I

then create new panels that only include the treatment municipalities and their matched control group.

Using these panels, I estimate the following regression:

𝑌𝑚𝑡 = 𝛼 + 𝛽𝑇𝑚𝑡 + 𝛾𝑋𝑚𝑡 + 𝜂𝑚 + 𝜆𝑡 + 𝜀𝑚𝑡 (5)

Equation (5) is in many ways similar to the baseline regression equation (2), but instead of

including municipality-fixed effects, I include match-fixed effects, 𝜂𝑚. The match-fixed effects are a

set of dummies that each takes on the value 1 for a treatment municipality and its matched control

municipalities. What happens is that each treatment municipality is paired with its matches in order to

isolate the within-matches variation. Thus, the difference-in-difference estimator 𝛽 compares the

average changes in expected outcomes between each treatment municipality and its matched control

group. The estimation of equation (5) is done using the same municipality-level clustered standard errors

as in the baseline difference-in-difference approach, to allow for autocorrelation within each

municipality over time.

When I use this matched difference-in-difference approach it is necessary to adjust the parallel

trends assumption to account for the propensity score matching. In any matching process, one need to

assume that conditional on the covariates, the potential average outcomes are independent of treatment.

However, with the matched difference-in-difference approach there may still be systematic differences

between treatment and control group due to time constant unobservable factors. Following Smith and

Todd (2005), for the difference-in-difference estimator in equation (5) to be unbiased it is necessary that

the following holds:

𝐸(𝑌𝑡0 − 𝑌𝑡−1

0 |𝑚𝑇 , 𝑃) = 𝐸(𝑌𝑡0 − 𝑌𝑡−1

0 |𝑚𝐶 , 𝑃) (6)

Equation (6) is basically a rearrangement of the parallel trends assumption in equation (4).

However, it now states that conditional on the propensity score, 𝑃, there would have been no systematic

differences in trends in student outcomes between a treated municipality and its matched control group

if treatment had not occurred. This means that conditional on the propensity score treatment becomes

as if randomly assigned.

As a final note, I want to mention that it is important to keep in mind that the matching process

creates the matched control group based on an estimation of the propensity score. This is true given that

nothing other than the pre-treatment covariates determines the assignment of treatment. It does not mean

that the municipalities in the matched control group is the most appropriate group to use when estimating

the true counterfactual effect. It is merely an estimation to create a control group that may be more

appropriate relative to the control group that includes all municipalities available.

more neighbors may increase bias due to the fact that each additional neighbor will by definition be further away in similarity

to the treated municipality. However, matching with replacement may reduce this bias since control municipalities that are

similar to many treated municipality can be used more than once. 12 The restriction is set by the data analysis software I use (STATA) and entails that m-neighbor must specify an integer greater

than or equal to 1 but no larger than the number of observations in the smallest treatment or control group.

- 20 -

6. Results

6.1 Difference-in-difference results

Tables 6 to 9 show the main results of my baseline difference-in-difference estimation. From these

tables we see that adding controls to the estimation causes the point estimates to change considerably in

magnitude. Some of the effects goes from being negative to positive and the majority of the point

estimates that are statistically significant turn insignificant when the controls are added. The conclusion

from this is that the effects are not robust to adding controls.

The controls are municipality-level student characteristics for the entire compulsory school

student population. I include them is because they may be correlated with treatment and determinants

for student outcomes. The fact that the point estimates change when the controls are added implies that

there are trends in the municipality demographics that covary with treatment. If this is true, there is risk

that the parallel trends assumption does not hold for my baseline approach. I therefore conclude that the

point estimates from the difference-in-difference estimation are too unstable to draw any causal

inferences from. In the next section I proceed to conduct the estimation with the match control group

sample, which might provide a better counterfactual.

Table 6. The effect of the public secondary school merges on final grade outcomes

(1) (2) (3) (4) (5) (6)

Average

GPA

Average

GPA

Share pass

all subjects

Share pass

all subjects

Share eligible

vocational school

Share eligible

vocational school

School Merge 6.34448*** -1.27710 -3.79141*** -1.74579 -3.63043*** -0.59773

(1.12327) (1.62727) (0.88028) (1.07557) (0.80625) (0.73332)

Female students (%) 0.88418** 0.29587 0.13711

(0.40296) (0.22285) (0.17157)

Students with migrant 0.31101*** -0.61143*** -0.64918***

background (%) (0.09887) (0.05322) (0.04576)

Students of parents with 3.35363*** 0.24584* -0.19628***

university education (%) (0.44943) (0.13179) (0.06161)

Constant 219.71255*** -8.33393 76.63152*** 61.60395*** 85.86972*** 102.88760***

(0.01448) (35.76285) (0.01135) (13.99783) (0.01039) (8.99046)

Observations 1,175 1,175 1,175 1,175 1,175 1,175

R-squared 0.00251 0.34649 0.00419 0.16531 0.00482 0.26157

Number of municipalities 235 235 235 235 235 235

Municipality Fixed Effects yes yes yes yes yes yes

Time Fixed Effects yes yes yes yes yes yes

Adjusted R-squared 0.00166 0.344 0.00334 0.162 0.00397 0.259

Robust standard errors in parentheses *** p<0.01, ** p<0.05, * p<0.1.

The table presents the results of the difference-in-difference estimation of the effect of secondary school mergers on the

municipality-level final grade results for the total 9th grade student population. Standard errors are clustered on municipalities.

The dataset includes 235 municipalities, of which six municipalities received treatment. All municipalities are weighted on

ninth-grade student population.

- 21 -

Table 7. The effect of the public secondary school merges on nat. stand. test average GPA

Robust standard errors in parentheses *** p<0.01, ** p<0.05, * p<0.1

The table presents the results of the difference-in-difference estimation of the effect of secondary school mergers on the

municipality-level average GPA on the national standardized tests in English, math and Swedish. Standard errors are clustered

on municipalities. The dataset includes 231 municipalities, of which six municipalities received treatment. All municipalities

are weighted on ninth-grade student population.

Table 8. Effect of public secondary school merges on the share of students that pass the tests

(1) (2) (3) (4) (5) (6)

English test English test Math test Math test Swedish test Swedish test

School Merge -0.226 0.197 -4.738*** -1.611 -1.039 -0.006

(0.607) (0.562) (0.962) (1.194) (1.341) (1.353)

Female students (%) -0.003 -0.324 0.338***

(0.079) (0.263) (0.116)

Students with migrant -0.135*** -0.588*** -0.164***

background (%) (0.020) (0.059) (0.029)

Students of parents with 0.066* -0.400*** -0.170***

university education (%) (0.039) (0.100) (0.040)

Constant 96.318*** 95.709*** 86.185*** 135.234*** 95.454*** 91.482***

(0.008) (4.745) (0.012) (15.115) (0.017) (6.349)

Observations 1,155 1,155 1,155 1,155 1,155 1,155

R-squared 0.000 0.059 0.003 0.095 0.001 0.093

Number of municipalities 231 231 231 231 231 231

Municipality Fixed Effects yes yes yes yes yes yes

Time Fixed Effects yes yes yes yes yes yes

Adjusted R-squared -0.000748 0.0559 0.00238 0.0922 0.000303 0.0901

Robust standard errors in parentheses *** p<0.01, ** p<0.05, * p<0.1

The table presents the results of the difference-in-difference estimation of the effect of secondary school mergers on the

municipality-level share of students that passed the national standardized tests in English, math and Swedish. Standard errors

are clustered on municipalities. The dataset includes 231 municipalities, of which six municipality received treatment. All

municipalities are weighted on ninth-grade student population.

(1) (2) (3) (4) (5) (6)

English test English test Math test Math test Swedish test Swedish test

School Merge 0.113 0.040 -0.665*** -0.104 -0.309 -0.462*

(0.257) (0.250) (0.205) (0.239) (0.260) (0.265)

Female students (%) 0.013 -0.043 0.058**

(0.019) (0.040) (0.027)

Students with migrant -0.018*** -0.099*** 0.010

Background (%) (0.005) (0.009) (0.007)

Student of parents with 0.076*** -0.085*** 0.061***

university education (0.013) (0.020) (0.020)

Constant 14.945*** 10.638*** 11.386*** 20.023*** 13.464*** 7.221***

(0.003) (1.277) (0.003) (2.475) (0.003) (1.726)

Observations 1,155 1,155 1,155 1,155 1,155 1,155

R-squared 0.000 0.091 0.003 0.127 0.002 0.046

Number of municipalities 231 231 231 231 231 231

Municipality Fixed Effects yes yes yes yes yes yes

Time Fixed Effects yes yes yes yes yes yes

Adjusted R-squared -0.000419 0.0874 0.00188 0.124 0.00121 0.0427

- 22 -

Table 9. Effect on the share of 7th grade students enrolled in public school sector

(1) (2)

Share 7th graders Share 7th graders

School Merge -2.322* -1.705

(1.184) (1.537)

Female students (%) -0.598

(0.501)

Students with migrant background (%) -0.052

(0.155)

Students of parents with -0.425

university education (%) (0.293)

Constant 78.519*** 133.076*** (0.020) (33.713) Observations 464 464 R-squared 0.003 0.041 Number of municipalities 93 93 Municipality Fixed Effects yes yes Time Fixed Effects yes yes Adjusted R-squared 0.00119 0.0323

Robust standard errors in parentheses *** p<0.01, ** p<0.05, * p<0.

The table presents the results of the difference-in-difference estimation of the effect

of secondary school mergers on the share of 7th graders enrolled in a municipality’s

public school sector. Standard errors are clustered on municipalities. The dataset

includes 93 municipalities, of which six municipality received treatment. All

municipalities are weighted on 7th student population.

- 23 -

6.2 Matched difference-in-difference results

In this section I will present the results of the difference-in-difference estimation with match-fixed

effects. As shown in equation (5) in section 5.3, each treatment municipality has been paired with its

matches in order to isolate the within-matches variation. In tables 10-13 the point estimates are in general

robust to adding controls. This is to be expected since the propensity score matching has been done in

part on these covariates. In addition, many of the results are now statistically significant. I will

henceforth treat the matched difference-in-difference approach as my main specification and treat tables

10 to13 as my main results. My inference will be done on the effects of treatment where the controls are

added.

Table 10 shows the matched difference-in-difference estimation of the effect of the public

secondary school mergers on the final grade outcomes. Column (2) shows the effect of the public

secondary school mergers on average GPA, which is negative and statistically significant on a one-

percent level. This result shows that the school merger reduced the average GPA in the municipality

with approximately 6.8 grade points. The final grade GPA ranges from 10 points to 340 points. From

the summary statistics table 3 we see that the mean average GPA in all Swedish municipalities is 219.8

points. Using this mean GPA as a baseline for comparison, the municipalities where the public

secondary school mergers were implemented should have a mean average GPA of 213 points. Hence,

the reduction of the average GPA compared to the national mean is not substantial. Nevertheless, the

effect still goes in the opposite direction of what should be the aim of the mergers.

Column (4) shows the effect of the public secondary school mergers on the share of students that

pass all subjects. This outcome can be seen as a measure that captures the effect of treatment on students

in the top of the skill distribution. Column (4) shows that the public secondary school mergers caused

the share of students that pass all subjects in the treated municipalities to decrease by approximately 3

percentage points. This result is statistically significant on a five-percent level.

Column (6) shows the effect of the public secondary school mergers on the share of students that

are eligible for vocational school education. To be eligible for a university prepatory program in upper

secondary school a student has to pass twelve out of seventeen subjects. Yet to be eligible for a

vocational school program the student only need to pass eight subjects. This outcome may therefore be

seen as a measure that captures the effect of treatment on students in the bottom of the skill distribution.

The public secondary school mergers caused the share of students that are eligible for a vocational

school education in the treated municipalities to decrease by approximately 3.12 percentage points.

Overall, the results show that the public secondary school mergers have a negative effect on the

average student academic performance. The results also show that the school mergers have a negative

effect on the share of students that pass all subjects and on the students that are eligible for vocational

school education. This tells us that the school mergers have a negative effect on the share of students

that perform well in school while it increases the share of students that will have insufficient amount of

passing grades to continue to any type of upper-secondary education.

- 24 -

Table 10. Match: effect of the public secondary school merges on final grade outcomes (1) (2) (3) (4) (5) (6)

Average GPA Average GPA Share pass

all subjects

Share pass

all subjects

Share eligible

vocational

school

Share eligible

vocational

school

School Merge -4.80930** -6.85423*** -2.17036 -2.96959** -2.11787** -3.11854***

(1.96141) (1.58724) (1.53822) (1.08111) (0.99324) (1.01127)

Female students (%) -0.48051 -0.31350 -0.33040

(0.69849) (0.45246) (0.35298)

Students with migrant -0.38653*** -0.41395*** -0.31014***

background (%) (0.13254) (0.10957) (0.05764)

Students of parents with 0.41958*** 0.02567 0.14621

university education

(%)

(0.14120) (0.09267) (0.08966)

Constant 204.77588*** 217.64812*** 74.40609*** 93.38755*** 87.96647*** 102.32726***

(1.35868) (34.38351) (1.35380) (22.81323) (0.85013) (16.94302)

Observations 155 155 155 155 155 155

R-squared 0.29892 0.40969 0.14659 0.29923 0.20555 0.36462

Number of municipalities 31 31 31 31 31 31

Match Fixed Effects yes yes yes yes yes yes

Time Fixed Effects yes yes yes yes yes yes

Adjusted R-squared 0.394 0.472 0.130 0.220 0.186 0.281

Robust standard errors in parentheses *** p<0.01, ** p<0.05, * p<0.1. The table presents the results of the difference-in-difference estimation with match-fixed effects. It show the effect of the

secondary school mergers on the municipality-level final grade results for the total 9th grade student population. Standard errors

are clustered on municipalities. The control group has been obtained through propensity score matching on pre-treatment

covariates. The match-fixed effects are a set of dummies that each takes on the value 1 for a treatment municipality and its

matched control municipalities. The match-dummy for Surahammar is the omitted baseline. The dataset includes 31

municipalities, of which six municipalities received treatment. All municipalities are weighted on ninth-grade student

population.

Tables 11 and 12 show the matched difference-in-difference estimation of the effect of treatment

on the standardized national test outcomes in English, math and Swedish. Table 11 shows the effect of

the public secondary school mergers on average test GPA. All effects turn statistically insignificant and

close to zero when the controls are added. The largest effect of the initiative on average test GPA is

found in column (4) where we observe that the mergers cause the math test average GPA to increase by

0.333 grade points. The national standardized test GPA ranges from 0 to 20 points. Summary statistics

table 3 shows that the national mean average GPA of 14.44 grade points. Compared to this, the mean

math GPA in the treated municipalities would be 14.77 points. This is not a considerable difference.

Table 12 shows the effect of the public secondary school mergers on the share of students that

pass the national standardized tests. The effect is again largest for the outcome on the math test. The

point estimate, shown in column (4), tells us that the public secondary school mergers increase the share

of students in the municipality that pass the national standardized tests in math with approximately 1.1

percentage points.

Overall the public secondary school mergers have small and positive effects on the national

standardized test outcomes. It is interesting that the effects of the school mergers on the national

standardized test outcomes goes in the opposite direction of the effects on the final grade outcomes.

However, all point estimates in tables 11 and 12 are statistically insignificant when the controls are

added to the estimation. The point estimates are so small in magnitude that it is unlikely that the effects

have any economic significance.

- 25 -

Table 11. Match: effect of public secondary school merges on nat. standard test average GPA

Robust standard errors in parentheses *** p<0.01, ** p<0.05, * p<0.1

The table presents the results of the difference-in-difference estimation with match-fixed effects. It shows the effect of the

secondary school mergers on the municipality-level average GPA on the national standardized tests in English, math and

Swedish. Standard errors are clustered on municipalities. The control group has been obtained through propensity score

matching on pre-treatment covariates. The match-fixed effects are a set of dummies that each takes on the value 1 for a treatment

municipality and its matched control municipalities. The match-dummy for Hedemora is the omitted baseline. The dataset

includes 35 municipalities, of which six municipalities received treatment. All municipalities are weighted on ninth-grade

student population.

Table 12. Match: effect of public sec. school merges on the share of students that pass the tests (1) (2) (3) (4) (5) (6)

English

test

English test Math test Math test Swedish test Swedish

test

School Merge 0.382 0.214 2.156 1.094 1.062* 0.589

(0.689) (0.593) (1.309) (1.528) (0.622) (0.604)

Female students (%) -0.043 0.142 0.219

(0.130) (0.578) (0.214)

Students with migrant 0.012 -0.305*** 0.009

background (%) (0.034) (0.100) (0.054)

Students of parents with 0.107*** 0.118* 0.182***

university education (%) (0.023) (0.068) (0.024) Constant 95.259*** 93.052*** 85.310*** 77.028** 94.621*** 76.749***

(0.910) (6.615) (1.972) (28.464) (0.764) (10.011)

Observations 175 175 175 175 175 175

R-squared 0.152 0.308 0.410 0.514 0.138 0.353

Number of municipalities 35 35 35 35 35 35

Match Fixed Effects yes yes yes yes yes yes

Time Fixed Effects yes yes yes yes yes yes

Adjusted R-squared 0.101 0.252 0.374 0.474 0.0850 0.301

Robust standard errors in parentheses *** p<0.01, ** p<0.05, * p<0.1

The table presents the results of the difference-in-difference estimation with match-fixed effects. It shows the effect of the

secondary school mergers on the share that pass the national standardized tests in English, math and Swedish. Standard errors

are clustered on municipalities. The control group has been obtained through propensity score matching on pre-treatment

covariates. The match-fixed effects are a set of dummies that each takes on the value 1 for a treatment municipality and its

matched control municipalities. The match-dummy for Hedemora is the omitted baseline. The dataset includes 35

municipalities, of which six municipalities received treatment. All municipalities are weighted on ninth-grade student

population.

(1) (2) (3) (4) (5) (6)

English

test

English test Math test Math test Swedish test Swedish test

School Merge 0.157 0.029 0.530** 0.333 0.156 0.004

(0.244) (0.172) (0.241) (0.275) (0.210) (0.164)

Female students (%) 0.012 0.021 0.042

(0.031) (0.094) (0.049)

Students with migrant -0.003 -0.041** -0.008

Background (%) (0.009) (0.017) (0.012)

Students of parents with 0.055*** 0.042*** 0.053***

university education (%) (0.006) (0.012) (0.006)

Constant 14.322*** 11.599*** 10.962*** 8.727* 12.723*** 8.669***

(0.369) (1.593) (0.313) (4.630) (0.251) (2.433)

Observations 175 175 175 175 175 175

R-squared 0.245 0.616 0.402 0.557 0.099 0.429

Numbers of municipalities 35 35 35 35 35 35

Match Fixed Effects yes yes yes yes yes yes

Time Fixed Effects yes yes yes yes yes yes

Adjusted R-squared 0.198 0.585 0.366 0.521 0.0443 0.383

- 26 -

In addition to examine the effect of the public secondary school mergers on student academic

achievement outcomes I want to investigate the impact on the share of students that are enrolled in the

public-school sector. Table 13 shows the effect of the mergers on the municipality-level share of 7th

grade students enrolled in public schools. The point estimate in column (2) shows that the public

secondary school mergers caused the share of 7th graders enrolled in the public-school sector in the

treated municipalities to decrease by approximately 10 percentage points. This result is statistically

significant on a five-percent level.

This tells us that the merging of the public secondary schools caused a smaller share of parents to

enroll their children in the public-school sector in 7th grade. The conclusion from this result is that the

municipalities seem not to have been successful in making the public-school alternative more attractive

by implementing the school mergers.

Table 13. Match: effect on the share of 7th grade students enrolled in public school sector

(1) (2)

Share 7th graders Share 7th graders

School Merge -10.371*** -9.981**

(3.683) (3.841)

Female students (%) -0.649

(0.801)

Students with -0.019

migrant background (%) (0.254)

Students of parents with -0.265

university education (%) (0.267) Constant 84.661*** 128.375***

(4.006) (33.751)

Observations 130 130

R-squared 0.278 0.309

Number of municipalities 26 26

Match Fixed Effects yes yes

Time Fixed Effects yes yes

Adjusted R-squared 0.217 0.231

Robust standard errors in parentheses *** p<0.01, ** p<0.05, * p<0.

The table presents the results of the difference-in-difference estimation with match-fixed

effects. It shows the effect of secondary school mergers on the share of 7th graders enrolled in a

municipality’s public school sector. Standard errors are clustered on municipalities. The control

group has been obtained through propensity score matching on pre-treatment covariates.

The dataset includes 26 municipalities, of which six municipalities received treatment.

All municipalities are weighted on ninth-grade student population

- 27 -

6.3 Heterogeneous treatment effects

In this section I will present the results of my heterogeneous treatment effect analysis. The aim of

this analysis is to examine whether the public secondary school mergers affect the students’ academic

outcomes in various ways due to their background characteristics. The estimation is done using the

matched difference-in-difference estimation specified in section 5.3. Just as in the main analysis the

point estimates in this section are robust to adding controls. This is reasonable since the propensity score

matching was done in part on the control variables. The tables in this section only includes the results

where the controls have been added.

Tables 14 to 16 present the point estimates of the effect of the school mergers on final grade

outcomes for the various student populations. The analysis is done with separate panels that differ in

size. Because of this, the results cannot be compared across panels. I have also included results from

estimating the effect of treatment on the outcomes for the entire student population. When comparing

these results it becomes obvious that the magnitude of this effect differs substantially across the tables.

Thus, the effect of treatment on the outcomes for the entire student population seems to be not be robust

to changes in the composition of the treatment and control group. These estimates also differ from the

main analysis results, presented in table 10. This suggest that my main results are sensitive to differences

in sample size and time period specification. I can therefore not say for certain that my analysis yields

the true magnitude of the heterogeneous treatment effects. I will however attempt to draw some

inferences about the direction of the effects. It is important to keep in mind that my heterogeneous

treatment effect analysis does not seem to be representative of my main analysis sample.

Table 14 presents the heterogeneous treatment effects on final grade outcome measures for the

female and male student populations. My results show that the public secondary school mergers have

an overall positive effect on the outcomes for female students. The school mergers have a negative effect

on male average GPA and the share of male students that pass subjects in the treated municipalities.

However, all the effects are close to zero and insignificant.

Table 15 presents the effect of the public secondary school mergers on the final grade outcomes

for students with different parental education levels. The first student population is ‘students of parents

with an upper-secondary school education’, which includes students for which the highest level of

education that both parents have is either a secondary school or an upper-secondary school education.

The second student population is ‘students of parents with a university education’, which includes

students who have at least one parent that attended university. Note that the panel used for this analysis

only includes the time period 2014/2015-2016/2017. Overall, the public secondary school mergers are

efficient in increasing final grade outcomes for students with parents that have at least an upper-

secondary school education. The overall effects of the school mergers on the final grade outcomes for

students with parents that have attended university are negative.

Table 16 presents the effects of the public secondary school mergers on final grade outcomes for

students with different native backgrounds. The first student population is ‘students with Swedish

background’, which includes students born in Sweden with at least one parent born in Sweden. The

second student population is ‘students with migrant background’, which includes students born abroad

who have migrated to Sweden. The results from table 16 show that the effects of the public secondary

school mergers on average GPA and the share of students that pass all subjects are negative and

statistically significant for both student populations in the treated municipalities. However students with

migrant background seem to be especially disadvantaged. The share of students eligible for vocational

school is reduced for both student groups. However, the effect is larger in magnitude and statistically

significant for students with migrant background.

As mentioned in section 4.3, the panel used for estimating the results in table 16 only includes three

treated municipalities. Because of this the treatment municipalities are matched with the three untreated

municipalities that have the closest propensity score. Hence, the sample is small and it is good to keep

- 28 -

in mind that the inferences I draw from table 16 may lack external validity. In essence, this means that

the results may not be applicable to student populations on a national scale.

Table 14. Heterogeneous treatment effects: female and male students

Average GPA Share pass all subjects Share eligible vocational school ed.

(1) (2) (3) (4) (5) (6) (7) (8) (9)

Total student

population

Female

students

Male

students

Total

student

population

Female

students

Male

students

Total student

population

Female

students

Male

students

School Merge -0.47913 1.13816 -1.46768 -0.61935 0.51509 -1.63239 0.35698 0.51569 0.61265

(2.29997) (3.20869) (2.10874) (1.36129) (1.24397) (1.63231) (1.16501) (1.06004) (1.41028)

Constant 163.75372*** 220.10257*** 153.48204*** 71.95804** 93.27816*** 62.89278 90.20224*** 106.77226*** 82.01550**

(43.62464) (55.52969) (44.23858) (32.99998) (29.03651) (39.58713) (25.63700) (23.62900) (30.94624)

Observations 155 155 155 155 155 155 155 155 155

R-squared 0.43951 0.40607 0.42207 0.31936 0.21620 0.35765 0.42459 0.29993 0.44973

Number of mun. 31 31 31 31 31 31 31 31 31

Controls yes yes yes yes yes yes yes yes yes

Match Fixed Effects yes yes yes yes yes yes yes yes yes

Time Fixed Effects yes yes yes yes yes yes yes yes yes

Adjusted R-squared 0.388 0.351 0.369 0.257 0.144 0.298 0.372 0.235 0.399

Robust standard errors in parentheses *** p<0.01, ** p<0.05, * p<0.1

The table presents the heterogeneous treatment effect results of the match difference-in-difference estimation for the female

and male student populations. Standard errors are clustered on municipalities. The dataset includes 31 municipalities, of which

six municipalities received treatment. The estimation is done with math-fixed effects. The match-dummy for Surahammar is

the omitted baseline. All municipalities are weighted on ninth-grade student population.

Table 15. Heterogeneous treatment effects: parental education level

Average GPA Share pass all subjects Share eligible vocational school ed. (1) (2) (3) (4) (5) (6) (7) (8) (9)

Total student

population

Students of

parents with

upper-sec ed.

Students of

parents with

university ed.

Total student

population

Students of

parents with

upper-sec ed.

Students of

parents with

university

ed.

Total student

population

Students of

parents with

upper-sec ed.

Students of

parents with

university

ed.

School Merge 0.45498 2.97003 -4.62459* 2.72206 4.87829*** -1.30829 3.04038* 4.52500** -0.50355

(3.92063) (3.93087) (2.35355) (2.15676) (1.68483) (3.65570) (1.72287) (1.87814) (0.95529)

Constant 206.94134*** 248.28899*** 235.29010*** 90.41178*** 124.26268*** 88.26894*** 81.93546*** 102.35472*** 79.05545***

(36.59284) (53.98529) (32.28426) (23.31593) (31.13542) (25.62171) (19.00266) (25.00144) (15.98070)

Observations 85 85 85 85 85 85 85 85 85

R-squared 0.38320 0.14810 0.36951 0.45213 0.27302 0.28449 0.52692 0.28517 0.31458

Number of mun. 15 15 15 15 15 15 15 15 15

Controls yes yes yes yes yes yes yes yes yes

Match Fixed

Effects

yes yes yes yes yes yes yes yes yes

Time Fixed Effects yes yes yes yes yes yes yes yes yes

Adjusted R-squared 0.299 0.0314 0.283 0.377 0.173 0.186 0.462 0.187 0.221

Robust standard errors in parentheses *** p<0.01, ** p<0.05, * p<0.1

The table presents the results of the match difference-in-difference estimation of the heterogeneous treatment effects for

students with different parental education level. Standard errors are clustered on municipalities. The dataset includes 15

municipalities, for which five municipalities received treatment. The estimation is done with math-fixed effects. The match-

dummy for Surahammar is the omitted baseline. This analysis deviates from the overall time period of this study as it only

includes the years 2014/2015-2016/2017. All municipalities are weighted on ninth-grade student population.

- 29 -

Table 16. Heterogeneous treatment effects: Swedish and migrant background Average GPA Share pass all subjects Share eligible vocational school

ed. (1) (2) (3) (4) (5) (6) (7) (8) (9)

Total

student

population

Students

Swedish

background

Students

migrant

background

Total

student

population

Students

Swedish

background

Students

migrant

background

Total

student

population

Students

Swedish

background

Students

migrant

background

School Merge -9.0177*** -8.4655*** -22.2502** -4.5848*** -3.72486** -10.3706*** -2.5571** -0.95203 -8.52463**

(2.65597) (2.46459) (8.14918) (1.30229) (1.34728) (2.46222) (0.95184) (0.80538) (3.70287)

Constant 48.84611 -46.31296 -228.44578 -

87.57863**

-

105.26161**

-12.49452 -37.24689 -53.45861* -179.41618

(76.24301) (63.50702) (241.13988) (35.16392) (36.81842) (132.41945) (27.32641) (23.95376) (108.74968)

Observations 50 50 50 50 50 50 50 50 50

R-squared 0.87036 0.85785 0.71374 0.73230 0.58500 0.63015 0.75380 0.64839 0.55691

Number of mun. 8 8 8 8 8 8 8 8 8

Controls yes yes yes yes yes yes yes yes yes

Match Fixed Effects yes yes yes yes yes yes yes yes yes

Time Fixed Effects yes yes yes yes yes yes yes yes yes

Adjusted R-squared 0.833 0.821 0.640 0.664 0.479 0.535 0.691 0.558 0.443

Robust standard errors in parentheses *** p<0.01, ** p<0.05, * p<0.1

The table shows the match difference-in-difference estimation of the heterogeneous treatment effects for students with Swedish

and migrant background. ‘Students with Swedish background’ includes students born in Sweden with at least one parent also

born in Sweden. ‘Students with migrant background’ includes student born outside of Sweden with both parents also born

outside of Sweden. Standard errors are clustered on municipalities. The dataset includes 8 municipalities, of which three

municipalities received treatment. All municipalities are weighted on ninth-grade student population.

- 30 -

7. Sensitivity analysis

7.1 Event studies

It is interesting to investigate the impact that the public secondary school mergers have over time.

This is because this capture both the pre-treatment trends and the yearly effects of treatment in the

aftermath of the public secondary school mergers. I do this by conducting multiple event studies. For

this analysis I use the data on the matched samples. I plot the difference-in-difference point estimates

where the binary treatment variable has been interacted with the years before and after the public

secondary school mergers were implemented. The year before the school merger was implemented, t-1,

is the omitted base category and is given by the dashed zero-line. In my analysis I compare the

coefficients to the zero-line. For example, a point estimate above the zero-line shows a positive effect

of treatment on outcome compared to the baseline year, and the opposite holds for a point below. The

event studies for each outcome measure are shown in figures 1 and 2.

Figure 1 – Event studies for final grade outcomes and the share of 7th graders in public schools

The graphs show the point estimates for the effect of treatment for each year. Year t-1 is the omitted category. The red line

represents that treatment was implemented one semester before the first outcomes are observed in the data. The t-2 point

estimates are based on outcome data from the municipalities that have two pre-treatment periods; Nyköping and Älmhult.

Consequently, these two municipalities are not part of the t+6 point estimates.

(a) Average GPA (b) Share students that pass all subjects

(c) share students elgibile for a vocational school education

(d) share 7th graders in public-school sector

- 31 -

Figure 2. Parallel trends plots – national standardized test outcomes

The graphs show the point estimates for the effect of treatment for each year. Year t-1 is the omitted category. The red

line represents that treatment was implemented one semester before the first outcomes are observed in the data. The t-2 point

estimates are based on outcome data from the municipalities that have two pre-treatment periods; Nyköping and Älmhult.

Consequently, these two municipalities are not part of the t+6 point estimates.

(a) English test – Average GPA (b) Math test – Average GPA

(c) Swedish test – Average GPA (d) English test – share of students that pass

(e) Math test – share of student that pass (f) Swedish test – share of students that pass

- 32 -

7.1.1 Parallel trends

The trust I can invoke in the results of my matched difference-in-difference estimation rests on

my key identifying assumption. It says that conditional on the propensity score there would have been

no systematic differences in trends in student outcomes between a treated municipality and its matched

control group if treatment had not occurred. This is essentially an extension of the parallel trends

assumption defined in section 5.2. If the effect of the school mergers on pre-treatment trends are

statistically insignificant it indicates that the assumption holds. I do not have enough pre-treatment data

to observe any trends, however I am able to observe one pre-treatment year, which is denoted t-2 in my

event study figures. If the coefficient for year t-2 is statistically insignificant, this provide some proof

that the parallel trends assumption may hold. Note that the effect in year t-2 is calculated based on the

municipalities that have two pre-treatment periods, and therefore the coefficient does not reflect the

whole treatment group.

The event studies in figure 1 show that for the majority of the outcomes the effect of treatment is

statistically insignificant in year t-2. It is only for the average GPA outcome that the coefficient is

significantly different from zero, which is the average GPA. Hence, this suggest that there are parallel

trends for the pre-treatment outcomes for the share of students in 7th grade measures and all final grade

outcomes except for the average GPA.

In figure 2 we see that the majority of the pre-treatment effects for the national standardized test

outcomes are statistically significant. The coefficients in year t-2 that are not significantly different from

zero are for the average GPA and the share that pass the national standardized test in English. Thus, the

parallel trends assumption seems to hold for the effects of the public secondary school mergers on the

national standardized tests in English, however not for the tests in math or Swedish. This is a sign that

the small and insignificant effects of treatment on the national standardized test outcomes presented in

my main analysis may be bias.

My baseline difference-in-difference estimation also rests on the assumption of parallel trends.

The fact that the results using this approach were unstable and insignificant indicates that the parallel

trends assumption may be violated. I have therefore conducted the same event studies using the same

data that I used in my baseline estimation. These are shown in figure C1, in appendix C. From these

figures we see that many of the pre-treatment effects are statistically significant, which further proves

that I cannot trust that the parallel trends assumption holds for my baseline difference-in-difference

estimations.

7.1.2 Dynamic treatment effects

The student cohorts may be affected differently by treatment due to their exposure time of

treatment. Thus, the magnitude of effect of the public secondary school mergers on student outcomes

may increase with time. For instance, the first student cohort exposed to treatment only attended 9th

grade in the merged school. It is likely that the magnitude of the effect of the school mergers is smaller

for this group than for the subsequent student cohorts. The effect of the mergers on the share of 7th

graders enrolled in the public-school sector may also be affected by exposure time to treatment. This is

because the parents may form different opinions about the merged public schools when they become

more established, which in turn may affect their choice of school for their children.

Panels (a), (b) and (c) in figure 1 show that the effect of the school mergers on the final grade

outcomes are initially positive but insignificant and close to zero. However, the positive effect turns

negative for the second student cohort, and the negative effect continue to increase in magnitude. For

the share of students that pass all subjects and the share of students that are eligible for a vocational

school education the point estimates seem to stabilize at a constant negative effect in year t+2, while the

negative effect of treatment on average GPA seem to continue to increase in magnitude.

- 33 -

As mentioned earlier, the effect of the school mergers on the share of 7th graders enrolled in the

public-school sector may also be affected by the exposure time. Panel (d) shows the effect of the school

mergers on the share of 7th grade students in the public-school sector. The point estimates are

continuously negative and increase in magnitude until year t+2. This serve some proof that a larger share

of the parents in the municipalities chose to enroll their children in independent schools instead of the

merged public school in the year that followed the implementation of the merger.

Figure 2 shows the event studies for the national standardized test outcomes. For most of the

outcomes the coefficients are initially positive, but declines over the years and turn negative in year t+2

or becomes zero in year t+3. The only effect of treatment that seem to be altogether positive is on the

share of students that pass the Swedish test. The fact that many of the coefficients are insignificant and

close to zero is in line with the main result findings.

7.2 Placebo tests on control variables

The controls that I include in the estimations are municipality-level student characteristics for the

entire compulsory school student population. The reason why I include them is because they are

potential determinants of the student outcomes and correlated with treatment. For example, there might

be positive trends in average GPA when the share of students with parents that have a university

education increases in the municipality because these students may possess certain abilities that cause

them to perform well in school. On the other hand, a municipality with a large share of student with

parents who have migrated to Sweden might also have a larger share of students enrolled in the public

school sector. This may be happen if there could exist information asymmetry between parents which

causes those who have never attended a school in Sweden themselves to not have full information about

the options that come with the ‘free choice’ principle.

In order to isolate the causal effect of the public secondary school mergers on student outcomes,

these variables need to be included and held constant in the regressions. The aim is to have conditional

mean independence; conditional on the control variables, the public secondary school mergers become

as if randomly assigned to the municipalities in question.

In this section I want to examine whether the municipality-level student characteristics change

when the public secondary school mergers are implemented. If this would be the case it implies that

treatment covaries with the municipality demographics. This might happen if residents with certain

characteristics move in or out of the municipality as a reaction to the merger. It might also happen if the

implementation of the public secondary school mergers happens because of the existence of certain

trends in municipality demographics. This means that because of the school mergers, the treated and

untreated municipalities experience different trends in student characteristics, which is an obvious threat

to the parallel trends assumption.

In order to test whether the municipality-level student characteristics covary with the school

mergers I perform a placebo test where I estimate the effect of treatment using the control variables as

the outcomes. The tests are done using the matched panels. Essentially, this is a test to see whether my

matching has been successful in creating a control group that works as a suitable counterfactual to the

treatment group. The results are shown in table 17. From this table we see that the public secondary

school mergers do not have a significant effect on the control variables. This is true for all panels. A

statistically significant effect of treatment on the control variables would have indicated that the effects

in the main analysis stems from changes in the municipality demographics that covary with treatment.

Instead, the results from my placebo tests points to the fact that the treatment and control group do

experience the same trends in municipality-level student characteristics. This result provides proof that

I have been able to isolate the causal effect of the school mergers on student outcomes by performing

estimations with my matched samples.

- 34 -

Table 17. Control placebo test Final grade outcomes panel National standardized test panel Share students in public schools panel

(1) (2) (3) (4) (5) (6) (7) (8) (9)

Female

students

(%)

Migrant

BG (%)

Parents w.

uni. ed.

(%)

Female

students

(%)

migrant

BG (%)

Parents w.

uni. ed. (%)

Female

students

(%)

Migrant

BG (%)

Parents w.

uni. ed. (%)

School Merge 0.424 -2.036 3.484 0.553 -2.425 2.064 0.124 -0.449 -0.028

(0.384) (2.316) (2.394) (0.496) (2.004) (3.163) (0.328) (1.005) (0.740)

Constant 48.139*** 11.574*** 35.114*** 48.781*** 10.709*** 39.081*** 49.008*** 18.288*** 43.702***

(0.322) (1.673) (1.529) (0.526) (1.434) (2.365) (0.171) (0.497) (0.261)

Observations 155 155 155 175 175 175 130 130 130

R-squared 0.215 0.300 0.256 0.134 0.277 0.151 0.128 0.745 0.359

Number of mun. 31 31 31 35 35 35 26 26 26

Match Fixed

Effects

yes yes yes yes yes yes yes yes yes

Time Fixed Effects yes yes yes yes yes yes yes yes yes

Adjusted R-squared 0.224 0.185 0.539 0.0812 0.233 0.0989 0.0927 0.735 0.334

Robust standard errors in parentheses *** p<0.01, ** p<0.05, * p<0.1

This table shows a placebo test of the effect of treatment on the control variables used in the main analysis. This is done using

the difference-in-difference estimation with match-fixed effects. Standard errors are clustered on municipalities. The panels

consist of six treated municipalities and the matched control groups. All municipalities are weighted on ninth-grade student

population.

7.3 ‘Worst case’ and ‘best case’ variables

In section 4.1 I discussed the issue of the ~100 values. When there are four students or less that

failed to become eligible for vocational school education or failed to pass the national standardized test

SIRIS denotes these variables with the value ~100.

In order to solve this issue I created two different types of measures for these outcome variables.

The first one is the ‘worst case scenario’ variable where I assume that four students fail to pass and then

calculate the true value of this case by dividing four by the student population and subtracting it from 1.

In the ‘worst case’ variable all the ~100 values are recoded with the value of my calculations. The second

one is the ‘best case scenario’ variable where I assume that all students pass, so I recode all ~100 values

to 100. The measure that I have used in all my estimations is the ‘worst case scenario’ variable since it

is likely that at least some students should fail to pass in each municipality. Yet it is interesting to conduct

estimations using both measures to see whether the effects differ.

I present the results of my baseline difference-in-difference estimation with the two outcome

variables in table D1 in appendix D.13 The point estimates do not differ in sign but there are some small

differences in magnitude. However, there is not one of the two outcome measure that consistently

produces a larger effect. Thus, the changes in magnitude seem to be arbitrary. Furthermore, the ‘best

case scenario’ variable tends to produce larger standard errors. From this I conclude that using the ‘worst

case scenario’ variable should not provide biased estimates over the use of the ‘best case scenario’

variable.

13 Table D1 only include the point estimates where no controls are added. The point estimates where controls are added did

not change my conclusion of the test. The same is true when running the matched difference-in-difference estimation on the

‘worst case’ and ‘best case’ variables.

- 35 -

8. Discussion and concluding remarks

The first aim of this study was to examine whether the public secondary school mergers were

efficient in increasing average student academic performance. For the municipalities that implement the

school mergers it is important that low-ability students get the help they need to pass secondary school

even though they attend a school with a larger number of students. Yet it is also important that the

students who would have performed well regardless of the initiative are not negatively affected by the

school merger. The results of my matched difference-in-difference estimation showed that the public

secondary school mergers had a negative effect on the municipality-level average GPA. The school

mergers also seem to reduce the share of students in the municipality that passed all subjects and the

share that were eligible for a vocational school education. This tells us that the municipalities that

implemented the school merger experienced a reduction in the share of students that resided in the top

of the skill distribution, while the share of students in the bottom increased. The take-home message

here is that the share of students that had the possibility to choose among a wide range of the upper-

secondary school programs shrank whilst the share of students that did not have enough passing grades

to continue on to upper-secondary school increased.

The second aim of this study was to examine whether a secondary school merger affects the share

of students that attend the public secondary school instead of choosing to enroll in an independent

school. I investigated this by estimating the effect of treatment on the share of 7th graders enrolled in the

municipality’s public-school sector. My results show that the public secondary school mergers caused

the share of 7th graders enrolled in the public-school sector to decrease by approximately 10 percentage

points. This implies that the initiative caused parents in the treated municipalities to seek another

alternative for their children rather than to enroll them in the merged schools. Along these lines, merging

the public secondary schools to one school does not seem to have made the public-school alternative

more competitive.

The trust that I can invoke in these results depends on whether the parallel trends assumption is

satisfied. The results of my event studies indicate that the assumption does not hold for all outcomes.

However, when I move on to conduct a placebo test on the control variables for the municipality-level

student characteristics the result shows that treatment has no statistically significant effect. It indicates

that treatment does not covary with municipality demographics in my matched panels. This seemed to

be an issue with my baseline difference-in-difference estimation. This provides some proof that the

treatment and control groups follow the same trends in pre-determined student characteristics. Hence

my matching strategy has created control groups that provide a more suitable counterfactual than using

all the municipalities with a constant number of secondary schools as controls.

Even though the positive effects of the school mergers on the students’ academic performance

seem to be absent, the initiative might still be an efficient desegregation tool. That is, if the school

mergers have a positive effect on academic outcomes for students who otherwise might experience

drawbacks from school segregation. I explored this by examining in what ways the public secondary

school mergers have heterogeneous treatment effects of the merger. My results show that public

secondary school mergers affect students’ final grade outcomes differently depending on their

background characteristics. However, my results also show that the effect of treatment on the outcomes

for the entire student population seems to be sensitive to changes in the composition of the treatment

and control group. I can therefore not say for certain that my estimations yield the true magnitude of any

heterogeneous treatment effects.

According to previous research, the student population that is negatively affected by school

segregation is students with a migrant background (Szulkin, Jonsson 2007; Nordin 2013; Grönqvist et

al 2015). The most prominent goal with the public secondary school merger in Nyköping municipality

was to reduce segregation among its youth population. This implies that the municipality was hoping

for an ‘integration effect’ which rests on the belief that the within-school peer effects are non-linear. In

- 36 -

other words, they believe that weak students experience positive effects from high-ability peers, while

high-ability students are not hurt by associating with low-ability classmates. The result of my

heterogeneous treatment effect analysis instead provides some evidence that the negative effect of the

school mergers on academic performance seem to be especially large for students with migrant

backgrounds. Due to the small sample size of the panel I use when I conduct this analysis it is good to

keep in mind that the magnitude of the true effect of the school mergers for students with migrant

backgrounds is uncertain and the results may lack external validity. However, there are some possible

explanations for why students with migrant backgrounds may not be benefiting from this type of

initiative. Firstly, creating one large public school in the municipality may not be the most efficient way

of helping students who might have a lower probability of scholarly success due to insufficient Swedish

language skills or other background factors. Potentially, this student population may benefit from

attending smaller schools where they will receive school resources that have a direct impact on their

academic performance. Secondly, under the assumption that students with migrant backgrounds would

benefit from attending a school with peers that have diverse backgrounds, the absence of the positive

impact of treatment on their academic performance might indicate that there is within-school segregation

that arises if the students form homogeneous sub-peer groups.

According to my results, the only group that seemed to benefit from the mergers is students of

parents who have at most an upper-secondary school education. The fact that students of parents with a

university education experience negative impacts from the merger may imply that these students benefit

from attending schools with a more homogeneous environment. These students would presumably have

attended a public school where students on average performed better than the municipality-mean if the

school mergers had not been implemented. Thus, in the absence of the initiative it is probable that these

students would have benefited from interacting with high-ability peers on a daily basis. The main results

indicate that the public school mergers had a negative effect on the share of students enrolled in public

schools. It might be the parents of students in the top of the skill distribution that choose to enroll their

children in independent schools instead. If the share of high-ability students in the public-school sector

is reduced the positive peer effects in the merged school one anticipated coming from this group might

be insufficient in increasing average student performance. I am not able to look at the heterogeneous

treatment effects of the school merger initiative on the share of students in the public-school sector. One

interesting contribution for future research is to explore whether the initiative caused students with

certain background characteristics to seek admission elsewhere. If parents with high socioeconomic

status choose an independent school for their children as a reaction to the school mergers, the initiative

may actually cause between-school sector segregation to increase rather than to eliminate it.

Investigating the effects of the public secondary school mergers on student outcomes has both

social and policy relevance. If the school mergers would have been successful in increasing the students’

academic outcomes it could have been an efficient and cost-reducing way for officials to handle the

potential imbalance in student performance across the public schools in a municipality. Furthermore, if

the school merger was in fact efficient in promoting integration there could have been positive outcomes

for students that are particularly hurt by school segregation.

The conclusion of this study is that the public secondary school mergers were not sufficient in

either increasing the municipality-level student outcomes on average, or the outcomes for the students

in the bottom of the skill distribution. This does not necessarily mean that students would not benefit

from efforts to eliminate school segregation, rather that this type of effort might not be enough to do so.

There is also the question of whether peer effects actually have an impact on students’ academic

performance. Sacerdote (2011) argues that while the large body of peer effects research has established

some evidence that peers affect an individual’s social outcomes, it is important to further examine

whether peer effects have any significant impact on educational outcomes. Implementing a merger of

all public secondary schools in a municipality seems to rest heavily on the idea that desegregation will

- 37 -

happen because of social interaction amongst students with diverse backgrounds. In order for students

to truly benefit from the peer effects that potentially emerge, there might also need to be resources spent

on eliminating within-school segregation. Thus, school officials might also need to create incentives for

students to interact with classmates that they do not share similar traits with. In this study I am not able

to draw inferences in what ways peers affect students within the merged public secondary schools, but

it is an interesting topic to explore in the future.

- 38 -

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- 40 -

Appendix A.

Table A1. Municipalities excluded from all control groups Municipalities with a decreasing number of

public secondary schools

Municipalities with an increasing number of public

secondary schools

Name: Official mun. key: Name: Official mun. key:

Boden 2582 Botkyrka 127

Enköping 381 Eskilstuna 484

Gävle 2180 Göteborg 1480

Huddinge 126 Järfälla 123

Härnösand 2280 Lerum 1441

Kiruna 2584 Lidingö 186

Kristianstad 1290 Lomma 1262

Landskrona 1282 Mark 1463

Leksand 2029 Nacka 182

Linköping 580 Sandviken 2181

Ludvika 2085 Storuman 2421

Lund 1281 Strängnäs 486

Mölndal 1481 Södertälje 181

Norrköping 581 Trelleborg 1287

Norrtälje 188 Umeå 2480

Pajala 2521 Uppsala 380

Sigtuna 191 Vänersborg 1487

Sjöbo 1265 Älvdalen 2039

Skövde 1496 Ängelholm 1292

Sundbyberg 183 Öckerö 1407

Timrå 2262

Täby 160

Upplands-väsby 114

Varberg 1383

Värmdö 120

Västervik 883

Västerås 1980

Östersund 2380

The table shows the municipalities that have been excluded from all the panels. The official municipality key is the

identification number of the municipality. The keys are decided by the Swedish tax office, Skatteverket.

- 41 -

Appendix B

Table B1. Matched control groups

Panel 1 - final grade outcomes

Nyköping Älmhult Örkelljunga

Gällivare 2523 Kinda 0513 Klippan 1276

Karlsborg 1446 Malung-Sälen 2023 Storfors 1760

Essunga 1445 Laxå 1860 Östra Göinge 1256

Torsby 1737 Berg 2326 Håbo 0305

Haninge 0136 Sävsjö 0684 Högsby 0821

Munkedal Surahammar Hedemora

Vindeln 2404 Kinda 0513 Jokkmokk 2510

Nora 1884 Malung-Sälen 2023 Haparanda 2583

Nordmaling 2401 Laxå 1860 Åstorp 1277

Gnesta 0461 Sävsjö 0684 Bjuv 1260

Överkalix 2513 Berg 2326 Simrishamn 1291

Panel 2 – share of students in a municipality’s public schools

Nyköping Älmhult Örkelljunga

Upplands-bro 0139 Haninge 0136 Hylte 1315

Ronneby 1081 Höör 1267 Tingsryd 0763

Kalix 2514 Sävsjö 0684 Gislaved 0662

Orust 1421 Ånge 2260 Östra Göinge 1256

Lilla edet Skara Hedemora

Nordanstig 2132 Höör 1267 Vilhelmina 2462

Övertorneå 2518 Haninge 0136 Nordanstig 2132

Simrishamn 1291 Trollhättan 1488 Jokkmokk 2510

Fagersta 1982 Överkalix 2513 Övertorneå 2518

Panel 3 – national standardized test outcomes

Nyköping Älmhult Örkelljunga

Ragunda 2303 Östra Göinge 1256 Storfors 1760

Sotenäs 1427 Fagersta 1982 Ovanåker 2121

Åstorp 1277 Simrishamn 1291 Bollnäs 2183

Vansbro 2021 Heby 0331 Bengtsfors 1460

Haninge 0136 Haparanda 2583 Hylte 1315

Munkedal Surahammar Hedemora

Osby 1273 Vellinge 1233 Håbo 0305

Hallstahammar 1961 Bjuv 1260 Ljusdal 2161

Åre 2321 Gislaved 0662 Klippan 1276

Arvika 1784 Jokkmokk 2510 Älvkarleby 0319

Köping 1983 Boxholm 0560 Heby 0331

Panel 4 – final grade outcomes divided on gender Nyköping Älmhult Örkelljunga

Båstad 1278 Mullsjö 642 Gnosjö 617

Karlshamn 1082 Gullspång 1447 Kramfors 2282

Halmstad 1380 Norsjö 2417 Tidaholm 1498

Svedala 1263 Mariestad 1493 Oxelösund 481

Sundsvall 2281 Gislaved 662 Bjuv 1260

Munkedal Surahammar Hedemora

Munkfors 1762 Högsby 821 Mullsjö 642

Borlänge 2081 Åmål 1492 Gnesta 461

Sävsjö 684 Oxelösund 481 Emmaboda 862

Markaryd 767 Fagersta 1982 Gullspång 1447

Vara 1470 Kramfors 2282 Norsjö 2417

- 42 -

Panel 5 – final grade outcomes divided on parental education level

Flen Götene Skara

Gnosjö 617 Klippan 1276 Övertorneå 2518

Malå 2418 Östra Göinge 1256 Simrishamn 1291

Fagersta 1982 Strömstad 1486 Töreboda 1473

Mellerud 1461 Ovanåker 2121 Alvesta 764

Burlöv 1231 Tranemo 1252 Tingsryd 763

Årjäng Säffle

Markaryd 767 Valdemarsvik 563

Falkenberg 1382 Hörby 1266

Sollefteå 2283 Hallstahammar 1961

Borlänge 2081 Ånge 2260

Hörby 1266 Orsa 2034

Panel 6 – final grade outcomes divided on Swedish and migrant background

Nyköping Älmhult Hedemora

Höör 1267 Solna 184 Klippan 1267

Helsingborg 1283 Vellinge 1233 Höör 1267

Vaggeryd 665 Osby 1273 Helsingborg 1283

- 43 -

Appendix C

Figure C1 – Event studies: baseline difference-in-difference panels

The graphs show the point estimates for the effect of treatment for each year. Year t-1 is the omitted category. The red line

represents that treatment was implemented one semester before the first outcomes are observed in the data. The t-2 point

estimates are based on outcome data from the municipalities that have two pre-treatment periods; Nyköping and Älmhult.

These two municipalities are excluded from the t+6 point estimates

(a) average GPA

(b) share pass all subjects

(c) share eligible vocational school education

(d) share 7th graders in public schools

(a) English test – average GPA

(b) English test – share pass

(c) Math test – average GPA

(d) Math test – share pass

(e) Swedish test – average GPA

(f) Swedish test – share pass

- 44 -

Appendix D.

Table D1. Difference-in-difference estimation: ‘worst case’ and ‘best case’ variables comparison

Robust standard errors in parentheses *** p<0.01, ** p<0.05, * p<0.1

The outcome variables denoted by ‘WC’ are the variables for which ~100 values are recoded under the assumption that four

students out of the municipality-level student population failed to pass the test. The outcome variables denoted by ‘BC’ is the

variable for which ~100 values are recoded as 100 under the assumption that no students failed. The estimation is done with

the baseline difference-in-difference estimation specified in section 5.1. Standard errors are clustered on municipalities. All

municipalities are weighted on ninth-grade student population.

Final grade outcomes panel National standardized test outcomes (1) (2) (3) (4) (5) (6) (7) (8)

Share eligible

voc. school

WC

Share eligible

voc. school

BC

share pass

English

test WC

share pass

English

test BC

share pass

math test

WC

share pass

math test

BC

share pass

Swedish

test WC

share pass

Swedish

test BC

School Merger -3.63043*** -3.63043*** -0.226 -0.635 -4.738*** -4.660*** -1.039 -0.724

(0.80625) (0.80625) (0.607) (0.820) (0.962) (1.018) (1.341) (1.537)

Constant 85.86972*** 85.95010*** 96.318*** 96.957*** 86.185*** 86.311*** 95.454*** 96.032***

(0.01039) (0.01039) (0.008) (0.011) (0.012) (0.013) (0.017) (0.020)

Observations 1,175 1,175 1,155 1,155 1,155 1,155 1,155 1,155

R-squared 0.00482 0.00440 0.000 0.001 0.003 0.003 0.001 0.000

Number of kommunkod 235 235 231 231 231 231 231 231

Controls no no no no no no no no

Muncipality Fixed

Effects

yes yes yes yes yes yes yes yes

Time Fixed Effects yes yes yes yes yes yes yes yes

Adjusted R-squared 0.00397 0.00355 -0.000748 -0.000315 0.00238 0.00207 0.000303 -0.000471

Root MSE 3.300 3.452 1.309 1.711 5.253 5.436 1.921 2.301

f-stat 20.28 20.28 0.139 0.599 24.24 20.96 0.600 0.222